U.S. DEPOSITORY
DEC 04 1978
 
 

   

TODAY'S MEDICINE,
TOMORROW'S SCIENCE

ESSAYS ON
PATHS OF DISCOVERY IN THE
BIOMEDICAL SCIENCES

AND
KAREN REEDS

Prepared Under Contract NO1-CO-55315
for the National Cancer Institute

JUDITH P. SWAZEY

DHEW Publication No. (NIH) 78-244

U.S. DEPARTMENT OF HEALTH, EDUCATION, AND WELFARE
Public Health Service National Institutes of Health

  
 

| 918
A Note on the Authors

Judith P. Swazey received her Ph.D. in the history of science from Harvard University.
She is a Professor in the Department of Socio-Medical Sciences at Boston University
School of Medicine and an Associate Professor in the Department of History, Boston
University. Her research and writing has dealt with the history of the neuro-sciences, the
processes of therapeutic innovation, and the social and ethical implications of contem-
porary biomedical developments.

Karen Meier Reeds received her Ph.D. in the history of science from Harvard University.
She has been a Mellon Postdoctoral Fellow at Bryn Mawr College and currently is a
Research Fellow at the University of California, Berkeley.

 
Preface

 

Today's Medicine, Tomorrow's Science is a study that grew out of the shared interest
of the National Cancer Institute's Program Analysis and Formulation Branch and the
authors in examining the ways that categorical or disease-oriented research have con-
tributed to the elucidation of fundamental biological phenomena and processes. For a
number of reasons, as we point out in chapter one, little attention has been paid to these
paths of inquiry and discovery while, conversely, the flow from basic research to applica-
tions in the understanding of disease processes and means of diagnosing, treating, or
preventing man’s ills has been charted frequently by analysts of science and medicine.

Throughout the course of preparing this volume we have received invaluable help from
many sources. The study was made possible by the initiative and support of Dr. Abraham
Cantarow, Dr. Robert Love, and Mr. Louis Carrese of the National Cancer Institute.

We extend our thanks to the following persons, who shared their expertise with us
by critically reviewing various chapters of the book: Dr. Garland Allen, Dr. Merriley
Borrel, Dr. Gerald Edelman, Dr. Virginia Fiske, Dr. Joseph Fruton, Dr. Diana Hall, Dr.
Vernon Ingram, Sir Rudolph Peters, and Dr. Frank Putnam. We are especially grateful
to Dr. Julius Comroe, who undertook the task of reviewing the entire manuscript for us.

“For their aid in preparing various portions and stages of the manuscript, our thanks
go to Consuelo Alvarez, Chris Suntala, Ruth McNeeley, and Phyllis Schiarizzi.

1899
Preface . .
Chapter 1.
Chapter 2.
Chapter 3.
Chapter 4.
Chapter 5.

Chapter 6.

Chapter 7.

On Blind Men, Elephants, and Floppy-eared Rabbits ......... 1
Louis Pasteur: Science and the Applications of Science ....... 11
Beriberi and the Coenzyme Function of Vitamin B; ......... 27
Disease and the Ductless Glands... ................... 53
“The Lesson of Rare Maladies:”” Sickle Cell Anemia and the

Genetic Control of Protein Structure ................... 73

A Crucial Experiment of Nature: Multiple Myeloma and the
Structure of Antibodies . . .. «is. vv vs sss rasan srs pews 93

Disease and DiSCOVEIY . + «cs vs sv nasmssssnnmnm ss annui 115
 
CHAPTER ONE
ON BLIND MEN, ELEPHANTS, AND FLOPPY-EARED RABBITS

The essays in this book revolve around a common
theme: many paths of inquiry and discovery about life
processes have begun through efforts to understand and
to intervene in states of disease. This route of inquiry
and discovery is a familiar one to those working in
clinical medicine and basic biomedical research, and to
historians of medicine and biology. But, at the same
time, it is a route that has received little more than
anecdotal mention in the literature on the nature and
history of scientific research. For that literature, by and
large, deals with what has become in many instances a
stereotyped view of how research and discovery proceed
— by some sort of necessary progession from disinterested
“pure’’ research to the application of the basic knowl-
edge thereby gained for the solution of “‘practical prob-
lems.” Such a progression, however, is neither necessary
or logical, but instead only one possible path to scien-
tific discovery, new knowledge, or the solution of
practical problems.

Our purpose in this study, initiated by the National
Cancer Institute, thus is to examine one aspect of the
complex paths of research, in the area of the biomedical
sciences. That aspect is the flow of interest and inquiry
that runs from a particular disease problem to major
advances in our understanding of fundamental biological
phenomena. Or, in abbreviated popular parlance, we are
mapping routes that run “from the patient's bedside to
the laboratory bench,” rather than the more frequently
discussed and charted routes from ‘‘the bench to the
bedside.”

After surveying a wide range of nineteenth and
twentieth century medical and biological work, we chose
a small number of disease-oriented research problems for
close historical study, utilizing primarily a detailed
tracing and analysis of primary sources. The examples
we selected, drawn from bacteriology, nutrition, bio-
chemistry, endocrinology, genetics, and immunology,
are presented in the form of case studies. In addition to
representing a range of biomedical inquiry that began
with a clinical problem, these cases illuminate other
aspects of the complex processes of research and dis-
covery. They represent, too, a variety of ways of examin-

ing and presenting historical materials in the. form of
narrative essays. For, we would argue, just as there is no
single way to ‘‘do’’ science, so too there is no single way
to describe how it was done.

Thus, our first case study deals with a particular
scientist, the illustrious Louis Pasteur, and focuses on
the early period of his career when he investigated dis-
eases of wine and vinegar. Many lessons emerge from the
story of Pasteur’s work, among them the variety of
interests and influences that shape an investigator's
work, the multiple interpretations that can be made
about that work, and the consequent difficulties, even
in historical retrospect, of neatly categorizing and
analyzing research in terms of its ‘‘applied’’ or “‘basic’’
nature.

Our second case study deals with a particular disease
rather than with a particular scientist. It documents how
efforts to understand and halt a ravaging disease, beriberi,
played a central role in the discovery of a class of sub-
stances vital to the animal economy, vitamins. Then, we
examine how subsequent research on the ‘‘beriberi
vitamin,”’ thiamin, helped to elucidate the biochemical
roles of vitamins, through a long and arduous series of
studies that led to the identification of thiamin as a
coenzyme in intermediary metabolism.

In the third case, we paint a broader canvas, looking
at a group of disease problems that, perhaps preemi-
nently, exemplify a flow of interest and effort “from the
clinic to the laboratory.” This case study shows, both in
broad outline and through particular examples, the
interrelations between the medical problems of diseases
of the “‘ductless glands’’ and the development of a major
field of biology and medicine, endocrinology.

Our final two case studies, like the beriberi study,
treat more specific disease problems, tracing how efforts
to understand their causes and nature led, in often
unforeseeable ways, to new understanding of funda-
mental biological phenomena. Thus, in Chapter 5 we
examine the role that work on sickle cell anemia played
in defining the genetic control of protein structure,
while in Chapter 6 we follow a trail of researches that
began in 1846 with the discovery of a strange urinary

 
product in a patient with multiple myeloma and ended
in the 1960’s with the first complete mapping of an
antibody’s molecular structure.

In our work, we have made no attempt to quantify or
specifically categorize the various lines of research we
examine, as has been done in some recent historical
studies. In our essays, indeed, we seldom use terms such
as basic or categorical research, for reasons that have to
do with two other themes or viewpoints running through
our study. The first of these, as we have noted, is that
there is no single path, no unique route, by which we
arrive at new knowledge of life processes, nor is there
a solitary path to knowledge of and means to prevent
or treat disease. Rather, as one begins to realize in think-
ing about the word biomedical, our understanding of
life processes, both normal and abnormal or diseased,
has come from many intersecting lines of research and
discovery. Some of these routes begin with research
efforts that are usually labelled as ‘‘basic’’ or ‘‘funda-
mental” — efforts said to be aimed primarily at improv-
ing our understanding of a particular phenomenon or
area of science, without regard for immediate practical
uses of that understanding. Other avenues in the bio-
medical arena begin with what today is called ‘‘categori-
cal” or “applied” research — inquiry that is centered
around one or more aspects of a disease (its etiology,
diagnosis, prognosis, or treatment). But whatever the
starting point, the end point of a given biomedical
research problem is seldom, if ever, reached by a straight-
line path of inquiry. And often, the end point can be
traced only in retrospect, for research frequently leads
its practitioners in directions that are hard to foresee
and, at the time, seemingly remote from the immediate
objectives of their work.

This view of biomedical research as a complex net-
work of processes and events, objectives and outcomes,
in turn bears upon another theme, the problems of
meaningfully labelling or characterizing biomedical
research activity with terms such as basic or applied. In
this first chapter, as a framework for the case studies
themselves, we will deal briefly with the why and what
of efforts to label types of biomedical research, and,
closely related to these efforts, with the oft misstated
role of chance or serendipity in research.

Blind Men and Elephants:
Labelling Biomedical Research

In the seventeenth century, historian Herbert Butter-
field has observed, the ‘proper method’ of scientific

inquiry was ‘‘one of the grand preoccupations, not
merely of the practicing scientist, but. . .amongst the
general thinkers and philosophers’’ (Butterfield 1958,
p. 97). Future historians, looking back upon science in
the latter decades of the twentieth century, may judge
that one of this period's ‘grand preoccupations’’ was
the nature of and relationship between ‘‘basic’’ and
‘applied’ research, or, in current biomedical parlance,
between ‘‘basic’’ or ‘‘fundamental’’ and ‘‘categorical’’
or “mission-oriented’’ research.

This issue is by no means a new one, for, as physicist
Alvin Weinberg reminded the participants at a 1966
conference on “‘the development and use of biomedical
knowledge,” ‘‘the argument about the relation between
applied and basic research. . .has been raging since the
1700°s"" (Weinberg 1967, p. 33). There are many rea-
sons, having to do with the history, sociology, and
philosophy of science, and with its practitioners and
patrons, for the origins and long persistence of this
argument. One set of factors, for example, related both
to perceptions about the nature of scientific discovery
and to the value system within the scientific community,
is a tradition of viewing ‘‘pure’’ research as a “*higher
form’ of intellectual activity than ‘‘applied’’ research.
“There exists in some circles,” Beveridge observed in
his noted text on The Art of Scientific Investigation,
"a certain amount of intellectual snobbery and tendency
to look disdainfully on applied investigation. This
attitude is based on the following two false ideas: that
new knowledge is only discovered by pure research
while applied research merely seeks to apply knowledge
already available, and that pure research is a higher
intellectual activity because it requires greater scientific
ability and is more difficult. Both these ideas are quite
wrong’ (Beveridge 1957, p. 169).

Both in the past and today, arguments about the
scientific and social roles of basic and applied research
also have involved practical quests for patronage — for
the support of researchers by public and private spon-
sors. In the recent history of biomedical research in the
United States, much (but by no means all) of the con-
cern about basic-applied distinctions has been linked
with the emergence of the federal government as the
major research patron in the years since World War II.
Social and economic policy decisions about how the
patron should disperse his finite monies among many
competing areas of research, in relation to various
desired outcomes of that research, have generated an
often heated dialogue about the nature of and “proper

 
balance’ among various lines of biomedical investiga-
tion, and have tended to foster a strict and competitive
division between basic and applied research.

To the extent that it revolves around funding con-
cerns, the basic-applied biomedicine debate has mounted
to new levels of intensity in the past decade. The princi-
pal catalyst was a statement made by President Lyndon
B. Johnson on June 15, 1966, on the occasion of the
Medicare program's debut. ‘’A great deal of research has
been done,’’ the President declared, ‘but. . .the time has
come to zero in on the targets. . .to get our knowledge
fully applied. There are hundreds of millions. . .spent on
laboratory research that may be made useful to human
beings if large-scale trials on patients are initiated in
programming areas. Now Presidents. . .need to show
more interest in what the specific results of medical
research are during their lifetime and during their
administration. . .And we are determined that the vital
link between pure research and practical achievement
will never be broken’ (Quoted in Weinberg 1967, p. 33).

President Johnson's interest in seeing biomedical
research ‘‘pay off’’ in terms of ‘reducing deaths and
disabilities’’ was scarcely a new concern at the upper
levels of government. Rather, it was one in a series of
statements and reports about the conduct of biomedical
research to and from the executive and legislative
branches of the federal government, that began in the
post-war years with Vannevar Bush's study for President
Roosevelt, released in 1945 as Science — The Endless
Frontier. Roosevelt had asked Bush for information and
recommendations on how scientific knowledge devel-
oped during the war could be rapidly applied for peace-
time uses, and how a national program of medical
research could be organized (Bush 1945). As one com-
mentator has remarked, “Science — The Endless Fron-
tier seems to have suffered the fate of many other
influential reports: often cited but seldom read.” Read-
ing it, one senses again how often history repeats itself,
as in Johnson's 1966 statement, and one can begin to
trace, over three decades, how “‘the conflicting ideas of
the relation of government to science and of the proper
function of science in American society became partisan
political issues in the years after 1945" (England 1976,
p. 46).

But if Johnson's call to ‘zero in on the targets’ was
not a new one, it was one that nonetheless had profound
effects on the givers and receivers of federal funds for
biomedical research. As Weinberg commented a few
months after the event, ‘‘the world of biomedical

research, at least that portion of it that regards itself as
following the Newtonian tradition of research for its
own sake, was thrown into a mild state of shock’ by
the President's remarks (Weinberg 1967, p. 32). In
retrospect, Johnson's remarks, and the responses to
them from within and without the biomedical research
community, was but one in a series of events and policy
decisions at the end of the 1960's that signalled the
start of a new fiscal and political era for biomedical
research. After two decades of burgeoning growth, with
the federal government as its major moral and financial
supporter, the research enterprise faced new delivery-
oriented competitors such as Medicare for the nation’s
health dollars (Berliner and Kennedy 1970). A series
of critical questions began to be asked, by many sectors
of society: about how research priorities were being or
should be decided, about the policy, or lack thereof,
that had guided federally funded research efforts, and,
as epitomized by President Johnson's statement, about
what the “health payoffs’’ had been from the massive
amounts of money, equipment, facilities, and manpower
devoted to biomedical research in the years since World
War II.

These and other questions about biomedical research
have continued to be asked, with increasing demands
for answers, in the 1970's. Thus, for example, the
Department of Health, Education, and Welfare’s ‘“For-
ward Plan for Health,” dealing with fiscal years 1976-
1980, noted that:

While there is no serious challenge to the assertion
that a major federal role in the health industry is
the support of basic biomedical and behavioral
research, there are growing concerns as to the size
and direction of that investment. For example,
there are current questions about how priorities
are set for biomedical research programs, why the
cost of doing research is climbing so rapidly, what
the appropriate relation should be between re-
search and health service needs, what the effect of
increasing pressure for targeted programs is, and
whether there is sufficient ‘‘balance’’ between and
around the various investment targets in the
research portfolio. (Quoted in Culliton 1974,
p.617)

Given the long history of concerns about defining the
“nature’’ and ‘‘proper methods’ of science, and the
more recent social and political history of biomedical
research, it is easy to understand why there has been of
late a ‘’grand preoccupation’ with the nature of and
relationship between “‘basic and applied’ research. And,
as one reviews the literature that this preoccupation has
generated, one appreciates Alvin Weinberg’s cautionary
words a decade ago: “that the question about the
basic-applied relationship is once more asked in sharp
and urgent terms, particularly with respect to biomedical
research, by no means implies that new or particularly
cogent insights have been attained’ (Weinberg 1967,
p. 33).

Indeed, especially when viewed in historical compass,
much of the discussion about the fundamental-categori-
cal nature of modern biomedical research is reminiscent
of the oft-told Hindu fable of the six blind men who
examined an elephant. The first man, falling against the
elephant’s side, bawled that an elephant is very like a
wall; a second, seizing a leg, declared the elephant to
be a kind of tree; another, grasping a tusk, held it to be
a spear; the fourth, feeling the trunk, knew it was like a
snake; the fifth man, feeling an ear, said the elephant
was like a fan; and the last man, holding the tail, pro-
nounced it just a rope. Each statement about the ele-
phant was a fair inference, but in sum they did not hang
together.

As they first approach the ‘‘biomedical research
elephant,” scientists and laymen alike generally feel they
will have little trouble in identifying a given part of the
elephant as ‘‘basic’’ or “‘applied.”” For if one views re-
search in any area of science as involving a spectrum that
runs from “very basic’ to ‘very applied,” it seems
evident that examples at either end of the spectrum
should not be hard to come by. But biomedical research,
a hybrid word fusing biological and medical, virtually
by definition involves human health/disease-related
objectives, however distant. It is a research enterprise
that fits well a conception of science that philosopher
Lewis Feuer has called ‘“‘predominantly that of the
utilitarian hedonist; the pursuit of science, apart from
joy in itself, is an instrument for the improvement of
the lot of mankind’ (Feuer 1963, p. 15).

For such reasons, even those involved in a given piece
of biomedical research may find it difficult to apply one
or another label to their activity. A simple but striking
discussion of this difficulty was given by Beveridge in
The Art of Scientific Investigation. Research, he ob-
served, is commonly divided into “‘applied’’ and “pure.”

This classification is arbitrary and loose, but what
is usually meant is that applied research is a delib-

\

erate investigation of a problem of practical impor-
tance, in contradiction to pure research done to
gain knowledge for its own sake. . .However, often
the distinction between pure and applied research
is a superficial one as it may merely depend on
whether or not the subject investigated is one of
practical importance. For example, the investiga-
tion of the life cycle of a protozoon in a pond is
pure research, but if the protozoon studied is a
parasite of man or domestic animal the research
would be termed applied. A more fundamental
differentiation, which corresponds only very
roughly with the applied and pure classification is
(a) that in which the objective is given and the
means of obtaining it are sought, and (b) that in
which the discovery is first made and then a use
for it is sought. (Beveridge 1957, pp. 168-69.)

Implicitly or explicitly, most commentators on the
basic-applied biomedicine issue end up, like Beveridge,
agreeing that there is at best an elusive dividing line
among types of biomedical research, and that many
different elements can enter into a given definition of
what part of the elephant is being grasped. The defini-
tion of a research project as basic or applied, for ex-
ample, may vary according to whether one’s primary
frame of reference is the problem being investigated,
the objective of the researcher, the locus and organiza-
tional form of the research, or the objective of the
research funder.

The struggle to carve up the biomedical research
elephant according to such variables has produced in the
past decade a profusion of studies, hearings, and reports
and a sometimes bewildering array of terms. Thus, one
can read discussions of basic research, fundamental
research, intrinsic basic research, mission-oriented basic
research, and non-mission-oriented basic research, and
how these endeavors may differ from applied research,
mission oriented research, targeted research, program-
matic research, systematic research, and categorical
research. And, in virtually every such discussion, there
are caveats about how difficult it is, in practice, to apply
these categories, about the complex feedbacks that
occur between the various suggested types, and about
the continuum that is biomedical research (see, for
example, Beecher, 1960; Bode 1965; Brooks 1965;
Comroe and Dripps 1974, 1976; Frederickson 1977;
Horsfall 1965; Kistiakowsky 1965; Shannon 1967;

Stewart 1965, 1967).

 
If the many past and present commentators on the
nature of biomedical research could be gathered together
to reach a consensus about the basic-applied argument,
we suspect that in the final analysis they would concur
with a statement by Paul A. Weiss, whose own investiga-
tions into morphogenesis have ranged from submicro-
scopic cellular biology to surgical methods for nerve
regeneration.

Unbroken lines of developmental changes (in
science) are apt to go unnoticed by those most
closely and continuously involved in them, and it
usually is left to the historians later to trace them
and package them artificially into separate epochs,
stages and phases.

A similar artifact is the customary categorical
distinction between ‘‘basic’’ and ‘‘applied” re-
search. No more realistic is the conceptual separa-
tion between ‘‘theory’’ and “‘practice”. . .All such
distinctions are a matter of degrees of interest and
focus and varying proportions in the mixtures of
methodologies applied, but certainly are not
properties of the subjects under study. As nature
knows no pigeonholes, so knowledge, and the
research leading up to it, constitute unbroken
continua. That is to say, no borders, fence posts,
or other signs of discontinuity are met along the
roads from. . .the most elementary discoveries in
the cellular and developmental biology of animals
to the prevention and cure of human disease.
Pigeonholing is plainly a managerial device for the
convenience, expedience and efficiency in handl-
ing practical affairs; in the infinitely graded
diversity of the real world, however, there is no
counterpart for the labels that designate the
various pigeonholes.

Of course, curious and purposeful investigators
and practitioners alike ignore straight jackets to
their thoughts and searchings imposed by extrane-
ous formalisms. They shuttle freely between the
“basic” and ‘‘applied”” directions of research
continuum. (Weiss 1971, pp. vii-ix)

As Weiss in part suggests, there are a number of
pragmatic reasons for making pronouncements about
the identity of whatever part of the biomedical research
elephant one is grasping. Each utterance may be a fair
inference for the time, place, and reasons it is made, but
in sum it is hard to make a whole elephant out of them.

The discussion and categorization doubtless will con-
tinue, but it would be well to bear in mind their history.
That history indicates that the efforts to categorize
various types of research often have little relation to the
actual doing of the research itself, nor that they will be
of great utility in predicting where a given line of re-
search will lead. As illustrated by the following two
statements, this has long been realized by many investi-
gators, and, more recently, by many who have sought to
determine the shape of a national research policy.

Biochemist Sir Edward Mellanby, in 1935: “It is
no more unlikely that discoveries of first-class
scientific interest will result from work directed
to the solution of practical problems of disease
than that discoveries of first-class interest to
medicine will result from the study of academic
physiological problems.” (Quoted in Platt 1956,
p. 399.)

Report of the Research Staff on National Goals to
the President, 1970: “The issue of the relevance
of scientific research to social needs is much more
complex than is often assumed. On the one hand,
there is no serious research, no matter how theore-
tical or basic in intention, which does not have
some potential for generating knowledge which
can ultimately lead to some socially valuable
application. On the other hand, the most deliber-
ately utilitarian research, whether basic or applied,
can yield results which have theoretical signifi-
cance. The history of science is one of reciprocity
between theory and experiment, between insight
and application, and between knowledge and
utility. It is misleading to conceive of a one-way
relationship, or to speak of research oriented
primarily to scientific knowledge in contrast to
science undertaken for the sake of its potentially
useful applications, as though they could be inde-
pendent activities. Whatever the primary motiva-
tion of the research project the results are likely to
include both, in difficult-to-estimate proportions.”
(Toward Balanced Growth 1970, p. 102)

Floppy-eared Rabbits and the Cult of Serendipity

In his 1945 volume of autobiographical essays, the
distinguished physiologist Walter B. Cannon included a
chapter entitled “Gains from Serendipity.” In it he dis-
cussed a long recurrent theme in literature on the nature
of science, a theme addressed particularly by scientists
themselves: the role of chance or accident in research
and discovery. Serendipity, Cannon noted, was not a
new term; it had been coined by Horace Walpole nearly
two hundred years earlier. But, until Cannon's essay,
serendipity was an almost unknown word, and the
great American physiologist surely had no prevision of
how it would become used and misused, and elevated
into a quasi-philosophical concept about a, if not the,
dominant characteristic of basic research.
In 1754, Cannon wrote,

2

Horace Walpole, in a chatty letter to his friend
Horace Mann, proposed adding a new word to
our vocabulary, “serendipity.” The word looks
as if it might be of Latin origin. It is rarely used.
It is not found in the abridged dictionaries. When
I mentioned serendipity to one of my acquain-
tances and asked him if he could guess the mean-
ing, he suggested that it probably designated a
mental state combining serenity and stupidity —
an ingenious guess, but erroneous.

Walpole’s proposal was based upon his reading of
a fairy tale entitled The Three Princes of Serendip.
Serendip, | may interject, was the ancient name
of Ceylon. “As their highnesses traveled,” so
Walpole wrote, “they were always making discov-
eries, by accident or sagacity, of things which they
were not in quest of.” When the word is men-
tioned in dictionaries, therefore, it is said to
designate the happy faculty, or luck, of finding
unforeseen evidence of one’s ideas or, with sur-
prise, coming upon new objects or relations which
were not being sought. (Cannon 1945, p. 68;
italics added)

The trouble with the use of serendipity since 1945
is that few of those who employ it seem to have read
Cannon, or his many predecessors who also commented
on the role of chance or accident in scientific investiga-
tions. Thus, too often, serendipity is described, as in a
popular book on the subject, as ‘the art of happy
accident,” leaving one with the impression that scientific
advances often are totally fortuitious, and that scientists,
like the three princes of Serendip, “just couldn’t miss
stumbling onto the most marvelous things even when
they werent searching for them’ (Halacy 1967, pp.
9-10).

In more sophisticated statements, scientists may not
be portrayed as people who blunder onto monumental
discoveries. But, in discussions of the differences be-

tween basic and applied research, serendipity often is
invoked as the distinguishing characteristic of basic
research, with little or no attempt to say what is meant
by ascribing a scientific advance as due to chance.
Rather, one usually reads simple declarative statements
to the effect that serendipity is a major avenue to new
knowledge or discovery in basic research, and hence the
directions or outcomes of basic research, to a large
extent, are uncertain, unpredictable, or uncontrollable
(in contrast, that is, to applied research, which is charac-
terized as being a programmatic or systematic progres-
sion toward clearly specified objectives). One of innu-
merable such characterizations of basic research is
found in the Department of Health, Education, and
Welfare's Forward Plan for Health, FY 1977-1981, in
the section on ‘relative investments in fundamental
and applied research.” ‘Effective ‘targeting’ of resources
to particular disease processes requires an adequate
fundamental science base to be effective, but articulate
exposition of the often serendipitous process of scienti-
fic advance is absolutely essential to greater public
understanding of this process’ (Forward Plan 1975,
p. 70).

What such cryptic allusions to serendipity leave out —
and they are critical omissions when the serendipitous
nature of basic research is argued in policy discussions —
is what it means to say that chance or serendipity plays
an important role in research. Yet, what it does mean
has been said, many times, by sociologists, historians,
and philosophers of science, and, most lucidly, by
scientists themselves.

The same year that Cannon wrote of serendipity,
for example, Robert K. Merton drew the attention of
sociologists of science to ‘‘the serendipity pattern,”
describing it as involving the “unexpected, anomalous
and strategic datum which exerts pressure upon the
investigator for a new direction of inquiry which extends
theory.” By strategic, Merton emphasized, he was
“referring rather to what the observer brings to the
datum than to the datum itself’’ (Merton 1957, p. 104).
For sociologists and their readers, Merton's point about
the importance of what the observer or investigator
brings to his chance encounter was given substance by
Barber and Fox's now classic study of ‘‘the case of the
floppy-eared rabbits.” Theirs was an account of ‘‘seren-
dipity gained and serendipity lost,” exploring the reason
why one clinical investigator pursued an unexpected
observation: after rabbits received an intravenous
injection of the proteolytic enzyme papain, their ears

 
collapsed. At about the same time, another researcher
independently made the same observation, but his
was an example of serendipity lost. Primarily because
of his “research preconceptions and the occurence of
other serendipitous phenomena in the same experi-
mental situation’’ he did not pursue the case of the
floppy-eared rabbits, which eventually led to new knowl-
edge about cartilaginous tissues (Barber and Fox 1957).

A central point about serendipity that emerges from
the sociological literature, then, is that while research
does involve the unexpected happening or chance
event, what happens as a result is not fortuitous, but
depends, for many reasons, upon what the investigator
brings to the occurrence of serendipity.

Scientists themselves have made this point repeatedly
as they have reflected on the role of chance in their
work. In an 1895 lecture on ‘‘accident in invention and
discovery,” for example, the great German physicist
and philosopher of science Ernst Mach said:

But granting that the most important inventions
are brought to man’s notice accidentally and in
ways that are beyond his foresight, yet it does
not follow that accident alone is sufficient to
produce an invention. The part which man plays is
by no means a passive one. . .In all such cases,
the inventor is obliged to take note of the new
fact, he must discover and grasp its advantageous
feature, and must have the power to turn that
feature to account in the realization of his pur-
pose. He must isolate the new feature, impress
it upon his memory, unite and interweave it with
the rest of his thought; in short, he must possess
the capacity to profit by experience. . .

The disclosure of new provinces of facts before
unknown can only be brought about by accidental
circumstances, under which are remarked facts
that commonly go unnoticed. The achievement
of the discoverer here consists in his sharpened
attention, which detects the uncommon features
of an occurrence and their determining conditions
from their most evanescent marks, and discovers
means of submitting them to exact and full
observation. (Mach 1943, pp. 266, 270)

The same thesis about the investigator's critical role in
ensuring gains from serendipity was stated briefly and
elegantly by Louis Pasteur: ‘‘chance favors the prepared
mind.” And, as Cannon noted, ‘Even before Pasteur,

Joseph Henry, the American physicist, enunciated the
same truth when he said, ‘The seeds of great discoveries
are constantly floating around us, but they only take
root in minds well prepared to receive them’’ (Cannon
1945, pp. 75-76).

Thus, as Beveridge wrote in describing and discussing
a range of unexpected discoveries, ‘the history of dis-
covery shows that chance plays an important part, but
on the other hand it plays only one part even in those
discoveries attributed to it. For this reason it is a mis-
leading half-truth to refer to unexpected discoveries
as ‘chance discoveries’ or ‘accidental discoveries’ "
(Beveridge 1957, p. 46).

Finally, if serendipity means chance occurrences
external to an investigator, which leads to an “‘unex-
pected discovery’’ only if the investigator is prepared to
notice, interpret, and act on the chance clue, is there
any reason why ‘‘serendipity’’ should be confined to
so-called “‘basic’’ research? The true meaning of “seren-
dipitous discovery’’ suggests not. And, indeed, the range
of examples of ‘‘chance discoveries’ cited by various
writers on the subject shows that they are not confined
to any one area of inquiry (see for example Beveridge
1957; Cannon 1945; Mach 1943; Taton 1962). Thus,
to cite a few examples, chance, coupled with keen obser-
vation and reason, entered into the discovery of electri-
city, the development of the wave theory of light, the
invention of the battery and the ophthalmoscope, the
discovery of sub-clinical conditions, penicillin, the
principles of immunization with attenuated pathogens,
and the invention of dynamite.

In sum, those who use, or more often misuse the
word serendipity, would do well to remember its history
and full meaning. If this were done, we might soon
disband what René Dubos has called “the cult of seren-
dipity.”’

When W. B. Cannon borrowed the word seren-
dipity from Horace Walpole, he used it merely
to symbolize the fact that scientific investigators
are likely to discover many interesting facts other
than the ones they are looking for. Oddly enough,
this simple concept has been given so much im-
portance and dignity during the past few decades
that it has become a dominant scientific philoso-
phy. If one were to judge from much recent
writing, even by some scientists, the justification
for doing research on almost any subject is the
statistical chance of achieving by accident, useful

 
and practical results. It would be out of place to
discuss here the historical fallacies on which this
belief is based. | cannot refrain, however, from
stating my view that the cult of serendipity is
based on an erroneous interpretation of the
history of science, and furthermore amounts to
an abdication of intellectual and ethical respon-
sibility. Serendipity is the equivalent of Stephen
Vincent Benet’s line, “We don’t know where
we're going, but we're on our way.” (Dubos 1967,
p. 128)

 
Chapter One
Bibliography

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Report to the President on the Research Programs of the
National Institutes of Health. 1967. Prepared Under the
Direction of the Office of Program Planning, National Insti-
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Basic Research and National Goals. A Report to the Committee
on Science and Astronautics, U. S. House of Representatives,
by the National Academy of Sciences. 1965. Washington,
DC: Government Printing Office.

Barber, B., and R. C. Fox. 1958. “The Case of the Floppy-Eared
Rabbits: An Instance of Serendipity Gained and Serendipity
Lost.” Amer. J. Sociol. 64:128-136.

Beecher, H. K., ed. 1960. Disease and the Advancement of Basic
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Berliner, R. W., and T. J. Kennedy. 1970. “National Expendi-
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Beveridge, W. |. B. 1957. The Art of Scientific Investigation.
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Bode, H. W. 1965. "Reflections on the Relation Between Sci-
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Brooks, H. 1965. “Future Needs for Support of Basic Research.”
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Bush, V. 1945. Science - The Endless Frontier: A Report to the
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Butterfield, H. 1958. The Origins of Modern Science. NY:
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Cannon, W. B. 1945. The Way of an Investigator: A Scientist's
Experience in Medical Research. NY: W. W. Norton & Co.

Comroe, J. H., and R. D. Dripps. 1974. ‘Ben Franklin and Open
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Dubos, R. 1967. ‘Opportunities and Pitfalls.” Research in the
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129.

England, J. M. 1976. ‘Dr. Bush Writes A Report: ‘Science - The
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Feuer, L. S. 1963. The Scientific Intellectual. The Psychological
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Frederickson, D. S. 1977. ‘Health and the Search for New
Knowledge,’ Daedalus (Winter): 159-170.

Halacy, D. S., Jr. 1967. Science and Serendipity. Philadelphia:
Macrae Smith Co.

Horsfall, F. L. 1965. “Federal Support of Biomedical Sciences.”
Basic Research and National Goals. Washington, DC: Govern-
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Kistiakowsky, G. B. 1965. “On Federal Support of Basic Re-
search.’ Basic Research and National Goals. Washington, DC:
Government Printing Office, pp. 169-188.

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Discovery.” Reprinted in Popular Scientific Lectures by
Ernst Mach. La Salle, IL: The Open Court Publ. Co., 1943,
pp. 259-281.

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to Application of Biomedical Knowledge.” Research in the
Service of Man: Biomedical Knowledge, Development and
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72-85.

Stewart, W. H. 1967. “An Inventory of Opportunities and
Cautions.’ Research in the Service of Man: Biomedical
Knowledge, Development and Use. Washington, DC: Govern-
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into Medicine. NY : Hafner Publishing Co.
CHAPTER 2
LOUIS PASTEUR: “SCIENCE AND THE APPLICATIONS OF SCIENCE"

During a long and productive career, Louis Pasteur
established himself as one of the most famous figures in
the history of science, one whose researches, cutting
across many fields of endeavor, had a profound impact
upon our health and understanding of a range of funda-
mental physico-chemical and biological phenomena.
Of the many topics which occupied Pasteur’s attention
during five decades, from the mid-1840’s to the late
1880's, he perhaps is best known for his work on the
causes and prevention of infectious diseases. In these
studies, he succeeded admirably in identifying the
microbes responsible for silkworm disease, anthrax,
chicken cholera, and swine erysipelas, and in develop-
ing means to prevent these and other major agricultural,
veterinary, and human diseases. Concomitantly, Pasteur’s
work on infectious diseases yielded basic techniques
for research in microbiology, the establishment of the
germ theory of disease, valuable insights into the phy-
siology of microorganisms, and the first workable
concepts of virulence and immunity.

An earlier and less familiar period in Pasteur’s career,
which we will examine in this chapter, was the research
on ‘diseases’ of wine and vinegar that occupied his
attention from 1855-1865. One familiar result of his
work during this time was the invention of “‘pasteuriza-
tion,” but that was only one of many remarkable accom-
plishments of this decade of intense work. Pasteur
himself saw his fermentation research as the indispensa-
ble prelude to his justly famous medical research. But
it resulted as well in a revolutionary new theory of
fermentation and putrefaction, a solid disproof of
spontaneous generation, and a new understanding of
the importance and ubiquity of microorganisms in
nature.

Our account of Pasteur’s 1855-1865 work, however,
will deal less with the outcomes of his experiments than
with their beginnings. We will consider the debated
question of why Pasteur chose this particular line of
investigation, given his earlier interests and his ideas
about the nature of life. And we will explore how
Pasteur’s feelings about the ‘‘proper conduct’ of scien-
tific research, and how tensions about the roles of and
relationships between ‘‘applied’’ and ‘‘basic’ research
in the mid-19th century, bore upon Pasteur’s own
interpretation of his work.

11

 

Pasteur’s work, as well as analyses of that work by
Pasteur and by his chroniclers, epitomize the difficulties
that can occur in attempting to unravel the relationships
between various lines of research, whether historical or
contemporaneous. His many biographers have treated
Pasteur as a pure scientist who kept getting ‘‘sidetracked”’
onto applied problems, as a ‘physician without a de-
gree,’ as a ‘free-lance of science,” and as an applied
scientist who made immensely fruitful fundamental
discoveries. These various depictions, however, are no
more ambivalent than Pasteur’s own views, as reflected
in his statements about the importance of his work
on industrial problems and disease. At times, he argued
that the pursuit of ‘practical applications of science’
could be a snare for the ‘‘servant of pure science.”
Thus, shortly after he had spent a triumphant week at
Emperor Napoleon II's palace in 1865, demonstrating
his discoveries on the microbial causes of wine and
silkworm diseases, Pasteur wrote to the Emperor that
the scientist who works on practical problems ‘‘clutters
up his life and thinking with preoccupations which
paralyze his faculty for discovery,’”” and he risks both
“his peace of mind and the success of his investigations”
(Pasteur, Correspondence 1/, 19 Dec. 1865, p. 237).

While in charge of the science faculties at Lille and
at the Ecole Normale in Paris, Pasteur campaigned in
favor of a strong emphasis on pure sciences in the
curriculum. The student who mastered the theory,
principles, and methods of pure science, he insisted on
many occasions, would have no trouble turning his
knowledge to applications in France's time of need.’
Yet, Pasteur himself taught very popular courses in
applied chemistry and worked on a long series of practi-
cal problems. And, as we read in his letters to Napoleon
111, the Emperor's Aide de Camp General Fave, and
various ministers of education he often justified his
requests for research funds by pointing to the immediate
economic or medical significance of his investigations.

Pasteur had a favorite and much-quoted aphorism,
that he used to underscore the primacy of pure science,
the trees whose fruit were the applications of science.?

’

There does not exist a category of sciences to
which we can give the name of ‘applied sciences.’
There are science and the applications of science.
But as we read this aphorism, and other statements
by Pasteur about “applied science,” it is important to
realize that he had a rather different understanding of
the term from our own today, an understanding condi-
tioned by the nature of and relationships between tech-
nology and science in the mid-19th century.3 Pasteur
considered the phrase ‘applied science’’ to be a “‘shock-
ing” and “false” combination of words. For, as tech-
nology and science were viewed at the time, it suggested
that the largely empirical discoveries of industry were
more than a mere “‘collection of recipes’’ and rules-of-
thumb; it suggested that they too could claim to rest
on the rigorous methods, theories, and experiments
that were seen as the foundations of pure science.

Pasteur’s formulation about ‘science and the applica-
tions of science” also had the advantage of making his
own work on industrial fermentations and the diseases
of men, animals, wines, vinegars, and beers appear an
indivisible part of his ‘“‘purely scientific’’ work on
crystals and spontaneous generation. It saved him from
feeling defensive about the years he devoted to practical
problems when he wished to regard himself as a “servant
of pure science.”

Pasteur’s earliest research, before his work on fermen-
tation, did not require him to cope with questions about
the ‘‘applied/pure’’ nature of his work that would
trouble him later in his career. As a student at Paris’
Ecole Normale Superieur from 1843-1846, he was
infected by his professors’ enthusiasm for the new
science of crystallography, which then offered physicists
and chemists one of the few ways to recognize and ob-
tain pure laboratory samples of a substance and to gain

knowledge of molecular structures (Burke 1966).%.

Pasteur’s entry into the field of crystallography began
at the end of 1846, when the chemist Auguste Laurent
joined the laboratory where Pasteur was working as an
assistant. Laurent asked Pasteur to assist him with some
experiments, and Pasteur recalled that ‘one day it
happened that M. Laurent — studying, if | mistake not,
some tungstate of soda, perfectly crystallized and
prepared from the directions of another chemist, whose
results he was verifying — showed me through the
microscope that this salt, apparently very pure, was
evidently a mixture of three distinct kinds of crystals,
easily recognizable with a little experience of crystalline
forms. The lessons of our modest and excellent professor
of mineralogy, M. Delafosse, had long since made me
love crystallography; so. . .I began to carefully study the
formations of a very fine series of combinations, all very

12

easily crystallized, tartaric acid and the tartrates.”
Pasteur continued: “Another motive urged me to prefer
the study of those particular forms. M. de la Provostaye
had just published an almost complete work concerning
them; this allowed me to compare as | went along my
own observations with those, always so precise, of that
clever scientist’ (Merz 1965, pp. 404-405).

In the course of these researches, Pasteur became
fascinated by the problem of explaining the relationship
between common tartaric acid and its isomer, racemic
acid (also called paratartaric acid), which possessed all
the chemical properties of tartaric acid but which
exhibited a strikingly different optical behavior in
polarized light.’ Pasteur examined crystals of racemic
and tartaric acid under the microscope with great care
and discovered in 1848 that racemic acid was in fact a
mixture of two crystals which were mirror-images of
one another. Moreover, one of these two crystals was
absolutely identical — in its crystalline geometry, its
chemical properties, and its response to polarized light
— to ordinary tartaric acid. From this discovery came
the realization that the left- or right-handedness of a
dis-symetrical (to use the word Pasteur coined to de-
scribe this special kind of asymmetry) crystal and its
underlying molecular structure can affect its physical
and chemical properties — the basis of stereochemistry
(Alworth 1972).

Both the ordinary right-handed crystals of tartaric
acid and the mixture of right-handed and left-handed
tartaric acid crystals in racemic acid were produced as a
by-product of the alcoholic fermentation of grapes.
Tartaric acid was commonly found as crystals on barrels
of wine, while racemic acid had only been found occa-
sionally and in small quantities. In 1852 Pasteur spent
a busy month visiting industrial refineries of tartaric
acid in hopes of discovering the conditions under which
the rare little tufts of racemic acid would form in the
midst of the large tartaric acid crystals. He was able to
establish that only the crude mother-liquors of tartaric
acid would produce racemic acid before the industrial
processes of refinement took place, but he still could
not say why racemic acid arose on the rare occasions
that it did. Instead, he went back to his laboratory at
Strasbourg, where he was now a professor of chemistry,
and there succeeded in turning ordinary tartaric acid
crystals into racemic acid by complicated chemical
manipulations.

In his work on tartaric acid and many other organic
compounds which also showed dissymetry, Pasteur

 
observed that only one kind of crystal was normally
found when these compounds occurred as natural
products of living things. Thus, the right-handed crystal
of tartaric acid was commonplace; its left-handed mirror-
image — either alone or in the racemic acid — was
exceptional. And, the right-handed one reacted differ-
ently with other optically active compounds from the
left-handed counterpart.

Having demonstrated with chemical reactions that
his structural principle of molecular dissymmetry
influenced chemical affinities, Pasteur began to speculate
about the cause of dissymmetry. Sharing the desire of
many 19th century scientists to find universal forces
or principles, Pasteur imagined that the dissymmetry
of organic compounds reflected a cosmic or universal
dissymmetry:

The universe is an asymmetric whole. | am inclined
to think that life, as manifested to us, is a function
of the asymmetry of the universe and of the
consequences it produces. The universe is asym-
metrical; for, if the whole of the bodies which
compose the solar system moving with their
individual movements were placed before a glass,
the image in the glass could not be superposed
upon the reality. Even the movement of solar
light is asymmetrical. A luminous ray never strikes
in a straight line upon the leaf where plant life
creates organic matter. Terrestrial magnetism, the
opposition which exists between the north and
south poles in a magnet and between positive and
negative electricity, are but resultants of asym-
metrical actions and movements. . .Life is domi-
nated by asymmetrical actions. | can even imagine
that all living species are primordially, in their
structure, in their external forms, functions of
cosmic asymmetry’’ (Quoted in Dubos 1950, p.
111).

Viewing the rotation of the earth and its magnetic
polarity as two possible dissymmetric influences on
living matter, Pasteur began to devise experiments to
see what happened to the dissymmetric chemistry of
plants when the earth's magnetic forces were reversed
by a solenoid or when the sun’s rays appeared to move
from west to east. Although his friends and mentors
begged him not to waste his time on research that
probably would lead nowhere, Pasteur had great hopes.
His wife wrote to her father-in-law during this period
that ‘‘Louis is rather too preoccupied with his experi-

13

ments. You know that those he is undertaking this year
ought to give us — if they succeed — a Newton or
Galileo’” (Pasteur, Correspondence /, 10 Nov. 1853,
p. 324).

The experiments, however, did not go well, and
Pasteur abandoned them for the time being. But he
never rejected the idea of a universal dissymmetry
manifested in the dissymmetry of living matter. Through-
out his career he returned to the subject, discussed it
in papers and public lectures, and picked up his aban-
doned experiments once more to distract himself from
the bitterness of France's defeat in the Franco-Prussian
War. At the end of his life he regretted that he had
not pursued the idea further, that he had not explained
the ultimate ‘‘cause of one of the greatest mysteries of
nature’’ (Pasteur, Correspondence I, 7 Dec. 1853, p.
325; P. Vallery-Radot, 1957°, p. 185).

In September 1854, Pasteur accepted the position of
professor of chemistry and dean of the new Faculty of
Sciences at Lille. Lille was the industrial center of north-
ern France, and the town itself had underwritten the
new science school in hopes of training its young men
in the theory and industrial applications of science.
The teaching in the school stressed practical matters
and thus ‘‘appeared to be the public's taste,” Pasteur
reported to his superior, the rector of the Academie de
Douai, in 1855 (Pasteur, Correspondence I, 26 Jan.
1855, p. 359). Pasteur’s course in chemistry attracted
the largest number of students and auditors — nearly
250, he boasted to a friend. He was particularly pleased
at the young men who had already finished their educa-
tion and started to work in industry, yet came to the
school to profit from studying in subjects most closely
connected to their future careers. There was, for ex-
ample, the son of a distillery owner who would take over
his father’s business in a few years; since he obviously
needed to know more chemistry than physics or natural
history, he was allowed to take the chemistry course by
itself and to pay reduced fees.

Pasteur’s mixed feelings about the relative importance
of pure science and applied science are revealed in his
correspondence and papers during his three years at
Lille. In his inaugurgl address as dean, for instance, he
first spoke eloquently to the citizens about the excite-
ment their sons would feel when they were introduced
to the daily utility: of science. “Where in your families
will you find a young man whose curiosity and interest
will not be immediately awakened when you put into
his hands a potato, when with that potato he may
produce sugar, with that sugar alcohol, with that alcohol
ether and vinegar?” (R. Vallery-Radot 1960, p. 75;
Pasteur, “Discours,”” 7 Dec. 1854, Oeuvres VII, pp. 130-
131). But, he hastened to add, “God forbid that theory
should ever disappear from this teaching. We must not
forget that theory is the mother of practice. Without
theory, practice is just routine born of habit.”

The Minister of Public Instruction, in fact, feared
that Pasteur would put too much emphasis on theory
at the expense of practical knowledge. Even while he
praised Pasteur’s teaching, the Minister urged him to
keep the industrial needs of the region constantly in
mind: “M. Pasteur must always guard against being
carried away by his love for science, and he must not
forget that the teaching of the Faculties, while keeping
up with scientific theories, in order to produce useful
results and extend its happy influence, should through
the most numerous applications adapt itself to the real
needs of the country” (Pasteur, Correspondence |,
p. 374 n. 1).

Pasteur apparently heeded his superior’s advice.
His activities at Lille included an analysis of fertilizers
at the request of the General Council of the Depart-
ment du Nord, which saw it as an important piece of
work in so rich an agricultural region, and also as an
opportunity to popularize and increase the influence
of the new Faculty. One Easter vacation was spent
in Belgium visiting metallurgical factories ‘‘since my
position as chemistry professor,” he wrote his father,
“requires | know a good deal about this’’ (Pasteur,
Correspondence 1, 11 Jan. 1856, p. 386; Nov. 1856,
p. 406). In 1855 and 1857 he offered a course on
“chemistry applied to industries’ which was received
with great enthusiasm by both his audience and the
Minister of Public Instruction. Every lesson was fol-
lowed by a field trip to a local factory where Pasteur
would discuss technical details and clarify the tech-
niques by drawing pictures on the blackboard (Pasteur,
“Compte Rendu des travaux de la Faculte des Sciences
de Lille pendant |'annee scolaire, 1855-1856," Oeuvres
Vii, p. 144-145).

Pasteur put a special emphasis on teaching about
and helping the sugar-beet industry of northern France.
A large part of his course on applied chemistry was
devoted to the details of the manufacture and refine-
ment of sugar and alcohol from beet juice. He was
impressed by the industry's eagerness to keep up with
scientific innovations and to adopt new processes.
But, he remarked in 1855, ‘a prejudice which must be

14

fought is this:. . .they are very disposed to believe that
there is an applied science, that the applications form
a separate body of doctrines, when really the applica-
tions of the sciences are nothing but deductions from
purely scientific discoveries’’ (Pasteur, Correspondence
/, 15 Nov. 1855, pp. 382-383). Much of Pasteur’s
later career confirmed his belief that ‘applications are
nothing but deductions from purely scientific discov-
eries.”” Yet, there is irony in the fact that this earliest
formulation of his aphorism about applied science
should concern the industry whose practical problems
were soon to stimulate Pasteur into entering the field
of biology and there making fundamental new discov-
eries.

In 1856 Pasteur’s interests in molecular dissymetry
and his responsibilities as a teacher of the practical
applications of science converged in the study of beet
juice fermentations. A student of his, Emile Bigo, had
tried to make vinegar from sugarbeet alcohol, but relying
only on the standard reference works and his notes on
Pasteur’s lectures, the young man had little success.
Pasteur wrote on his behalf to a friend, a physics profes-
sor at Nancy, to enquire about a method of preparing
vinegar using beechwood shavings that Pasteur had seen
at the friend's brother-in-law’s house (Pasteur, Corre-
spondence /, July 1856, p. 394-395). We do not know
what became of young Bigo’s experiments on vinegar
in Pasteur’s laboratory, but Pasteur’s encouragement
and interest in his attempts had important consequences.
Bigo’s father — the owner of a beet juice distillery in
Lille — sought Pasteur’s help on a problem he was having
in his factory. The sugarbeet juice was not fermenting
into alcohol, but into lactic acid.

Pasteur soon was so absorbed with the puzzle brought
to him by the elder Bigo that he went to the factory
every day; Madame Pasteur complained wryly that he
was living “neck-deep in beet juice’’ (Pasteur, Correspon-
dence I, 10 Dec. 1856, p. 412). Pasteur’s early experi-
ences with a microscope now proved its value. He spent
long hours comparing samples of beet juice and testing
one idea after another. On the first day he began study-
ing the fermenting juice, he observed little globules
which grew and budded in the liquid. In the samples of
juice that were producing the unwanted lactic acid, he
soon noticed another kind of globule, smaller and
longer than the globule he found in the healthy vats.
Grasping the practical implications of his observations,
Pasteur told the Bigos to test the healthiness of the
fermentation by watching the shape of the microscopic

 
globules; if they were large and round, the fermentation
was going well; if they became elongated, lactic acid
fermentation was replacing the desired alcoholic fermen-
tation (R. Vallery-Radot 1960, p. 79; P. Vallery-Radot,
19582, p. 10).6

We have little information about this period in
Pasteur’s career, and it is not clear just when and how he
realized that the two kinds of globules he saw in the
fermenting beet juice were in fact living organisms and
the cause of the fermentations. His reports on his
investigation to the Society of Science in Lille only
described his chemical analyses of the fermentations,
and not his microscopic studies. He told his students
“how the ferment looks under the microscope’’ but
did not suggest that the globules were alive and actively
making the juice turn to alcohol or lactic acid (P. Vallery-
Radot, 19582, p. 10). Pasteur, however, was predisposed
to consider such an explanation, even though it directly
opposed the two prevailing theories of fermentation
championed by the most influential chemists of the
day, Liebig and Berzelius.” Berzelius regarded the
yeast of alcoholic fermentation as simply a kind of
chemical catalyst; Liebig believed that yeast caused
fermentation by its disintegration and decomposition,
which in turn disturbed the sugar molecules so that
they broke down into alcohol. Pasteur, though, had
long been convinced that the dissymmetry of organic
molecules was somehow directly correlated with the
fact that they were produced by living — not disinte-
grating — entities. In 1855, after giving up his romantic
experiments on the ultimate cause of molecular dis-
symmetry, he had gone back to studying examples of
organic compounds which exhibited optical activity.
Amy! alcohol was a case which especially aroused his
curiosity, because it did not behave according to the
rule he had formulated for tartaric acid and similar
compounds. Amyl alcohol showed optical activity,
rotating polarized light like tartaric acid, but its crystals
did not show the dissymmetric structures Pasteur
expected.

Lille provided Pasteur with ample opportunity to
study amyl alcohol, for it was a common by-product
of several industrial fermentations, including the beet
juice lactic acid fermentation which was giving M.
Bigo such trouble. Pasteur did not take long to decide
that Liebig's explanation of amyl alcohol’s optical
activity was untenable. Liebig argued that optically
active sugar molecules, excited by the disintegration
of the unstable yeast, broke down into amyl alcohol

molecules which preserved the optical activity of the
precursor. Pasteur voiced his opposition to Liebig’s
views in an 1857 ““Memoir on Lactic Acid Fermenta-
tion, ’ which he presented to the Society of Sciences,
Agriculture, and Arts of Lille. In his Memoir, which
Bulloch characterizes as epitomizing ‘‘the essential
points of all Pasteur’s work on fermentation, and indeed
of bacteriology,” Pasteur argued as follows (Bulloch
1938, p. 60).

The molecular constitution of sugars seems to me
to be very different from that of amyl alcohol.
If this alcohol, when active, originated from sugar,
as all chemists agree, its optical activity would
derive from that of sugar. | am loath to believe
this, considering the present state of our knowl-
edge, for every time that one tries to find the
rotatory property of a substance in its derivatives,
it promptly disappears. The fundamental mole-
cular group must remain in some measure intact
in the derivative if the latter is to continue opti-
cally active, a result that can be foreseen from my
investigations, since the property of optical
activity is entirely due to a dissymmetric arrange-
ment of elementary atoms. But | think that if
the molecular group of amyl alcohol does derive
from sugar, it is too distantly connected to retain
the dissymmetric arrangement of atoms. (Pasteur,
“Memoire sur la Fermentation appele lactique,”
1857, Oeuvres, Il, pp. 3-4; Conant 1952, p. 25)

What then in the beet juice was responsible for altering
the arrangement of the sugar molecule?, Pasteur asked.

Pasteur confessed that his preconceived ideas about
the role of molecular dissymmetry in the ‘organization
of living organisms’’ led him to examine the juice under
the microscope for living organisms. In the grey nitro-
genous scum on the top of the juice, he discerned
“little globules or very short segmented filaments,
isolated or in clusters,” which he admitted would look
very like tiny bits of disaggregated protein to anyone
who was not forewarned! But he then invented inge-
nious techniques for isolating and growing these little
globules in a pure state, and demonstrated that lactic
acid fermentation took place whenever a trace of the
living grey deposits was sown in a suitable mixture of
alkaline liquid and sugar.

In his first paper on fermentation in 1857, Pasteur
told his audience in Lille how his earlier study of amyl
alcohol had made him ask about the process of fermen-

 
tation that gave rise to amyl alcohol, how he was men-
tally prepared to find living organisms, how he isolated
and grew the lactic acid ferment, and how he could
always produce lactic fermentation (and no other kind)
whenever he put the globules into the proper medium.
To the naked eye, he said, this newly discovered ferment
resembled in appearance and activity the well-known
product of alcoholic fermentation, brewer's yeast. Each
of the two ferments, however, was absolutely specific:
pure lactic acid ferment never caused alcholic fermenta-
tion, and pure brewer's yeast never produced lactic acid.
Moreover, the two throve in different conditions: brew-
er’s yeast grew best and turned sugar to ethyl alcohol
most efficiently in a neutral medium, while the globules
of lactic acid ferment preferred an alkaline environment.
Most important, the yeast or ferment had to be alive.
The process of fermentation, Pasteur affirmed, was
simply a manifestation of the globules’ living organiza-
tion, development, and physiological activity, and not,
as Liebig held, a sign of their death and putrefaction.

Not long after presenting this paper on lactic acid
fermentation, Pasteur observed something that clearly
demonstrated the intimate connection between fermen-
tation and molecular dissymmetry. He noticed that a
solution of racemic ammonia tartrate (ammonia par-
atartrate) lying about in his laboratory had become
moldy and begun to ferment.® Such accidents were
common enough, but at this point any kind of fermen-
tation would have attracted Pasteur’s eager attention.
To his great satisfaction, he found that the mold was
choosing between the two forms of ammonia tartrate,
fermenting the right-handed one and leaving the left-
handed one alone. It was a far easier way to isolate the
left-handed isomer than the elaborate chemical techni-
ques Pasteur had worked out a few years before. He was
so pleased with this elegant finding that he submitted
a paper about it to the illustrious Academy of Sciences
to be considered for the Prize in Experimental Physiol-
ogy. He received the prize early in 1860 for his work
on fermentation in general, but this observation won
special mention from Claude Bernard and the other
judges. When he reviewed his life work many years
later, Pasteur ignored his interest in amyl alcohol and
M. Bigo’s request for help and made it sound as if his
discovery of this signal fact was what had led him from
crystallography to the study of fermentations (P. Vallery-
Radot 19582, p. 12; Pasteur, “La Dissymetrie Molecu-
laire,”” 1883, Oeuvres 1, p. 376).

16

Pasteur had no doubt that every kind of fermentation
or putrefaction required its own peculiar microorganism.
Between 1857 and 1863, he published paper after
paper identifying these specific living agents of fermen-
tation and describing the conditions they required for
survival. One of these papers, published in 1861, is
particularly notable. In the course of systematically
studying the products of lactic acid fermentation,
Pasteur noticed that the microorganisms associated
with the formation of butyric acid from lactic acid
behaved differently from the infusoria now familiar
to him from a variety of fermentations. When he watch-
ed the infusoria of the lactic acid ferment move about
ina drop of liquid under a coverslip, he could see them
cluster about the edges of the coverslip. But the butyric
acid infusoria appeared to shun the edges of the cover-
slip. He followed up this observation with experiments
which demonstrated that the butyric acid ferment could
live in the absence of free oxygen, and that, in fact,
oxygen would kill the tiny microbes. Turning back to
consider the oxygen needs of other ferments, Pasteur
came to the conclusion that “fermentation was life
without air.” Some microbes, like the butyric acid
ferment, were strictly anaerobic (a word coined by
Pasteur): they could live and produce butyric acid only
in the absence of oxygen. Most microbes, though, were
aerobic: they preferred to live in the presence of oxygen,
yet they too could survive without oxygen by ferment-
ing, by breaking down organic compounds in their
environment to obtain the energy they needed to live.

Yeast, Pasteur found, can live either aerobically or
anaerobically, and in studying the conversion of sugar
into alcohol and yeast protoplasm by yeast grown with
and without oxygen, he discovered what later was
termed the ‘‘Pasteur effect’’: sugar is converted into
yeast protoplasm more efficinetly under aerobic condi-
tions than anaerobically, but, for complex reasons, the
actual utilization of sugar is lowered.’ The Pasteur
effect subsequently was demonstrated in freshly picked
fruit by Pasteur in 1872, and then in frog muscle tissue
by Paschutin in 1874. The mechanism of the Pasteur
effect continues to intrigue physiologists and bioche-
mists to this day, and it surely counts as one of the most
interesting basic discoveries to come out of Pasteur’s
research on fermentation.

During these years in which Pasteur generalized the
phenomenon of fermentation, he also worked hard on
two closely related lines of research. In the fall of 1857,
he was given the important post of director of scientific
research studies at his beloved Ecole Normale Supérieure
in Paris. His official duties no longer required him to
worry about the practical problems of industrial fermen-
tations, but a similar problem of even greater economic
importance was soon set before him: what caused the
diseases of vinegars and wines?

Pasteur’s earliest research on this subject may have
been inspired by a kind of local patriotism. For in 1858
he wrote a friend that he was taking a microscope with
him on his trip home to Arbois in order to study the
grape-must disease, ‘which requires my presence in
Arbois throughout the month of September’ (the
month of the grape harvest). The first spoiled wines
Pasteur looked at were those of his native Jura vine-
yards, and in them he spied microorgnaisms similar to
the lactic acid ferment he had discovered the year before
(Pasteur, Correspondence 11, 28 August 1858, pp. 35-36;
“Introduction,” Oeuvres, 111, p. V).

He did not, however, spend much time just then on
the maladies of wine and vinegar, because the fundamen-
tal assumption of his experiments on fermentation was
under attack, and Pasteur became embroiled in one of
the now classic controversies in the history of science.
In maintaining that each kind of fermentation and
putrefaction was caused by a specific kind of living
microorganism — the germ theory of fermentation —
Pasteur had implicitly ruled out the possiblility of
spontaneous generation of microscopic life. For if
microbes could come into life from the random jostling
of organic matter in the course of decomposition and
fermentation, then there was no sense to the specific
actions of the ferments that Pasteur had watched with
such care. In 1858, a professor of medicine in Rouen,
Felix Pouchet, presented his ‘proofs’ of spontaneous
generation before the Academy of Sciences in Paris; a
year later he described his experiments and metaphysical
ideas about the spontaneous generation of microorgan-
isms in an immense book, Heterogenie. Pasteur’s direct
involvement in the debate stirred up by Heterogenie
began when Pouchet asked him in a private letter wheth-
er he thought the lactic acid ferment might not be spon-
taneously generated. Pasteur replied that there was not
as yet enough evidence to say, and that Pouchet might
have been too hasty in asserting the reality of spon-
taneous generation, given the ease with which microbes
like the lactic acid ferment could contaminate the air
and the broths of organic matter from which the micro-
bes has seemingly been created (Farley and Geison 1974,
p. 179).

After this polite response, Pasteur joined the debate
in earnest — much against the advice of his friends. In
1860-1861 he published five papers on his spontaneous
generation experiments, which have become justly
famous for their elegance and meticulous technique.
He drew out the necks of glass flasks of boiled broths
into long curves which allowed air to flow in easily, but
which caught the dust-motes, germs, and spores in the
air on the damp sides of the neck: the broths remained
perfectly clear. He carried flasks of sterile broths high
into the Alps to prove that, even in the mountain air,
germs could contaminate the broths, and also that some
samples of mountain air were completely germ-free.
(Pasteur, ‘‘Memoires sur les corpuscles organisees qui
existent dans |'atmosphére,’”” 1861, Oeuvres, Il, pp.
210-294; Conant 1953).

Pasteur’s carefully designed and executed experi-
ments dealt several damaging blows to the theory of
spontaneous generation, and the observations and
experiments on which it rested. Pasteur, for example,
demonstrated that micororganisms or their germs
floated in the air, whereas Pouchet only claimed that
the ‘“‘eggs’’ or ‘‘germs,’” rather than the adult microbes,
came into being spontaneously from decomposing
organic matter. He showed too that air alone could not
initiate the generation of living things, as Pouchet and
others had argued, and that simple measures of heating
and air filtration could prevent ‘organic broths’ like
those prepared by Pouchet from showing any signs of
life.

The question of spontaneous generation was [ut
before a commission of the Academy of Sciences for
a decisive judgment in 1864. The dramatic clarity of
Pasteur’s experiments, his scornful condemnations of
Pouchet’s logic and technique, his self-assured explana-
tions of his own results, and finally Pouchet’s affronted
withdrawal from the official demonstrations of the
major experiments, convinced the commission that
spontaneous generation did not occur. Another round
of the controversy, with the English physician, Henry
Charlton Bastian, defending spontaneous generation,
took place in the 1870s, but for the time being Pasteur
could consider the question settled triumphantly in his
favor and he could give more time to his work on the
diseases of vinegars and wines (Duclaux 1920, pp. 109-
111; Farley and Geison, 1974, p. 161-198).

Pasteur’s researches on the diseases of vinegar and
wine were a logical but not a necessary sequel to his
general studies of fermentation and spontaneous genera-
tion. In his Studies on the Mycoderms: The Role of

 
These Plants in Acetic Fermentation, delivered at the
Academy of Sciences in February 1862, Pasteur ex-
plained that he had long suspected that microscopic
fungi were involved in the production of vinegar from
wine (i.e., acetic acid from alcohol):

In the researches on fermentations which | have
pursued for many years now, various indications
led me to think that the mycoderms could not be
alien to the formation of acetic acid. These indica-
tions multiplied and defined themselves more and
more; | applied all my efforts to follow them up
with direct experiments. (Oeuvres, 111, pp. 7-12)

Indeed, he had started noticing these ‘‘indications’’
even before he started his work on alcoholic and lactic
fermentation. As we have seen, young Emile Bigo had
tried to produce vinegar while working in Pasteur’s lab at
Lille in 1857, and Pasteur had then sought information
from his friends about processes for making vinegar. It is
clear from Pasteur’s first report on acetic fermentation,
to the Chemical Society of Paris on July 26, 1861, that
he had fully expected what he found: a microscopic
fungus, mycoderma, covered the wine's surface with a
delicate transparent film and turned the alcohol into
vinegar. The German process in which the wine was
poured over beechwood chips entirely depended on the
presence of this fungus on the chips. The beechwood
chips had no mysterious catalytic property, as Liebig
and many other eminent chemists had maintained in
their textbooks.!! Six months after this first report,
Pasteur patented a reliable method for sowing the
mycoderm into wine and then put the process into the
public domain. No longer would the vinegar-makers of
Orleans have to wait anxiously for the thin veil of the
fungus to establish itself by chance.

Pasteur’s long memoir of 1864 on acetic fermenta-
tion, vinegar, and the mycoderma simply elaborated the
points he had made in the first paper, for by this time
his interest had shifted to the maladies of wine. Pasteur’s
1866 book, Studies on Wine, Its Diseases, and Causes
Which Provoke Them, with new processes for conserv-
ing and aging wine, opened with a dedication to Napo-
leon 111:

In the month of July 1863, the Emperor urged me
to turn my researches toward the understanding of
the diseases of wines. Directed by observations of
detail which my studies on fermentations had sug-
gested to me, | had already caught sight of the

possibility of a worthwhile piece of work on this
subject, to which | have dedicated myself ever
since with the thought of his concern for one of
the greatest agricultural products of France and
with the desire to respond to the kindness of an
August patron. (Pasteur, Etudes sur le vin, Oeuvres
111, pp. 112-113)

Although occupied with his work on fermentation
and his experiments on spontaneous generation, Pasteur
had begun thinking about the diseases of wines several
years before the Emperor made his suggestion. In 1858,
we have noted, he had examined diseased wines from his
native countryside, and in 1859 he had justified his fer-
mentation studies to the Minister of Public Instruction
by pointing out a practical result of his research: healthy
wine contained not only alcohol, but also hitherto un-
suspected by-products of fermentation such as glycerine
and succinic acid, which helped give wine its ‘pleasant
properties.” Then, in 1861, his friend, the chemist
Balard, asked Pasteur to look at some diseased wines
from the vineyards of Montpellier; Pasteur was pleased
to recognize the micro-organisms he had seen in the Jura
wines. And, of course, Pasteur’s work on acetic fermen-
tation was, in effect, a study of the commonest ailment
of wines, their souring and turning to vinegar. But the
Emperor's encouragement — and the financial support
that it implied — made Pasteur set to work in earnest in
1863.

During the wine harvests of 1863 and 1864, Pasteur
and a small band of his favorite former students left
Paris for the wine growing regions ‘‘to watch the fer-
mentation practices . ., to study diseased wines on the
spot, and to collect the observations and views of men
competent in these matters’ (Pasteur, Correspondence
/1, 14 July 1863, p. 125). As he had expected, he was
soon able to associate every malady and evil taste of
wine with its own microorganism. One turned the wine
sour, another made it bitter, yet others made it ropy or
oily. Given an apparently healthy sample of wine, he
could predict from microscopic studies of its alien
ferments among the yeast globules just how it would
taste in a few days. At the same time, he showed that
the only rationale for the traditional fear of air reaching
the wine was that the air could carry in the germs of
these diseases; otherwise, oxygen actually helped healthy
wine to mature in flavor and color. Moreover, just like
the yeast, the undesirable ferments were normally pres-
ent on the grapes themselves. If the diseases were to be

 
prevented, the parasitic microorganisms had to be killed
or weakened without destroying the wine at the same
time.

Pasteur first experimented with tasteless antiseptic
agents (inorganic phosphates and sulphates), but with no
great success. He then turned to heat, for his experi-
ments on spontaneous generation had proven that heat
could kill microbes. Although centuries of tradition
forbade heating wine, Pasteur tried the experiment and
announced the happy results to the Academy of Sci-
ences in May 1865, less than two years after acting on
the Emperor's suggestion. Wine heated to 50-60°C,
well below boiling, did not lose its flavor or color and
it did not spoil (Duclaux 1920, pp. 141-144; Pasteur,
“Nouvelles observations au sujet de la conservation des
vins,”” 1865, Oeuvres Ill, pp. 418-422). He patented
the technique of heating the wine and put the process
in the public domain, as he had done with his vinegar
processes. The technique was quickly dubbed “‘pasteuri-
zation” and used for all kinds of perishable foods and
liquids. That fall the Emperor invited Pasteur to spend
a week at the palace, where the scientist gave himself
the pleasure of showing Napoleon Ill that the micro-
organisms of wine diseases could be found even in
bottles from the Imperial cellars (Pasteur, Correspond-
ence //, November-December 1865, pp. 216-238).

To us, it sounds odd to call an unwanted change in
fermentation a ‘‘disease,’”” but the usage goes back to
antiquity. Indeed, men had often tried to cure diseased
wines with the same remedies they used to cure their
own ailments (Majno 1975, pp. 221-224). Linked to
this was another traditional analogy: the corruptions of
contagious disease were like the ‘‘metamorphoses of
fermentation’ and putrefaction. In ancient medicine a
whole class of diseases were labeled “‘putrid diseases,”
as Pasteur reminded the Academy of Sciences in 1863,
and to him these connotations of ‘‘disease’’ and ‘‘fer-
mentation” were tremendously suggestive. As early as
1859, he was arguing to the Minister of Public Instruc-
tion and to the Emperor himself that fermentations,
putrefactions, and contagious diseases played similar
parts in the “unending circle of life and death’ and that
they owed their existence to similar causes (Pasteur,
“Note remise au Ministre de I'Instruction publique et
des cultes,” 1859, Oeuvres I1/, 1. 481). This became a
constant theme in his progress reports to the Minister
and Emperor during the early 1860's.

However, even though Pasteur recognized the “‘inter-
est and ability”” of research on the general problem of

19

infection by microorganisms, he did not enter the field
of his own accord. Until 1865, using a strategy common
to scientists seeking funds for their work, he was content
to appeal to the possible medical applications of his
work to justify to his sponsors the costs of his researches
on fermentation and spontaneous generation. The
year 1865, however, marked an important turning point
in Pasteur’s career. Until then he could consider himself
a chemist who “‘happened’’ to work on problems that
involved living matter. But, while Pasteur was still en-
grossed in the details of pasteurization, he was suddenly
asked by his beloved teacher, J. B. Dumas, to investigate
a disease of higher organisms. Pasteur’s student and
assistant, Emile Duclaux, vividly recalled the day when
his master was asked to find out what was killing silk-
worms and ruining the economy of southern France.

. . .Pasteur, returning to the laboratory, said to me
with some emotion in his voice: “Do you know
what M. Dumas has just asked me to do? He
wants me to go into the South and study the
disease of silkworms.”” | do not recall my reply;
probably it was that which he had made himself
to his illustrious master: “‘Is there then a disease
of silkworms? And are there countries ruined by
it?” (Duclaux 1920, p. 145)

Pasteur protested his complete ignorance of silk-
worms to Dumas, expressing astonishment, according
to one anecdote, at learning that inside every silk cocoon
there is a silkworm turning into a moth! Dumas only
replied, “So much the better! For ideas you will have
only those which shall come to you as the result of your
own observations’ (Dubos 1950, pp. 213-214).

From then on, Pasteur worked primarily on prob-
lems of infectious disease, first dealing with two epi-
demics which were simultaneously devastating the silk-
worm industry, then anthrax in cattle, fowl cholera,
swine erysipelas, and finally rabies in dogs and people.
The twenty years that Pasteur spent on medical research,
years in which he contributed signally to the rise of
medical bacteriology and the development of immu-
nology, were a splendidly successful elaboration and
application of the ideas and techniques he had worked
out during the previous ten years of fermentation
research.

The year 1865, then, is an appropriate place to close
our account of Pasteur’s early career, and to turn to a
discussion of the pattern of his discoveries during the
years of crystallographic and fermentation research.
Pasteur’s published scientific papers and lectures offer
us many statements of his views on the subject. To the
modern reader, Pasteur’s papers — written for oral
delivery before scientific societies — seem astonishingly
informal and conversational in style, including incidental
remarks that no scientist today would be able to publish.
The reports of the experiments frequently lack the
measurements and details of technique that other
researchers would need to duplicate them. Pasteur
prefaced many papers with comments about the line
of thought or preconceived ideas that had led to the
experiments at hand, and ended them with speculations
about the ultimate significance of the results. René
Dubos has wittily imagined how an editor of a scientific
journal today would react if young Pasteur had sent
him that first paper on lactic fermentation:

“Dear Dr. Pasteur,” the editor would write, ‘‘you
have observed a few interesting phenomena, but
your account of them is almost useless for lack of
precise description and of quantitative data.
Furthermore, you would do well to dissociate
more clearly than is done in your paper well-
established facts from your personal opinions
concerning the nature of life processes. Allow me
to tell you, for your own good, that these roman-
tic opinions are entirely out of place in a dignified
scientific paper — enjoyable as they may be when
heard over several glasses of beer or wine in the
twilight of an evening's conversation.” (Dubos
1958, p. 16)

Pasteur, however, used his autobiographical and meta-
physical digressions to immense rhetorical effect, for
such artless candor about the workings of a scientist's
mind could not fail to charm his audiences. It is very
easy to see from his papers why his lectures were so
popular.

By continually harking back to his earlier work,
Pasteur acted as his own historian. He often claimed
that his life's work had been guided by the principle of
molecular dissymmetry which he had discovered in his
early crystallographic studies of racemic acid. In 1883
he wrote in a memorable passage: “Carried on, en-
chained should | say, by the almost inflexible logic
of my studies, | have gone from investigations of crystal-
lography and molecular chemistry to the study of fer-
ments; | have been engrossed with the thought of admit-
ting dissymmetry into chemical phenomena’’ (Pasteur,
“La dissymetrie moleculaire,’”” 1883, Oeuvres I. p. 736).

20

Similarly, when he jotted down an outline in 1877 for
a possible book on ‘’Studies on contagious or transmis-
sible diseases,”” he reminded himself to include his 186Q
memoir on alcoholic fermentation, his reports on
anaerobic fermentation, and his studies of the diseases
of wines and silkworms (Oeuvres, VI: intro., p. V).
Because the germ theory of contagious disease was so
clearly implied by these earlier researches, he believed
they would make the best, the most logical introduction
to the projected book. In his own reconstruction of his
researches, the immediate reason for Pasteur’s actually
commencing work on infectious disease — Dumas’
urgent request that he study the dying silkworms —
seemed to be beside the point. Sooner or later, he
implies, something would have provided a similar occa-
sion for starting research on diseases of animals and men.

Given Pasteur’s training and orientation as a nine-
teenth century French scientist, his Cartesian insistence
that “logic’’ determined the sequence of his work is not
surprising, and his retrospective arguments to that effect
are very persuasive. His grandson’s seven volume edition
of Pasteur’s collected works was designed to underscore
the rational unity that Pasteur saw in his researches;
each volume’s introduction comments directly on the
formidable logical chain that binds all of Pasteur’s work
together. ’

René Dubos, however, makes two cogent criticisms
of Pasteur’s belief that he was pushed by ‘‘an almost
inflexible logic”’ to make the discoveries he did. First,
Dubos points out, the origins of the ideas owe little to
logic but a great deal to intuition, keen observation, and
bold guessing. “‘In the work of Pasteur, logic is evident
in the demonstration and exploitation of his discoveries
rather than in their genius. It is the phase of his work
devoted to the development of his ideas which makes
the bulk of his long papers, and which gives the impres-
sion of orderly logical progression” (Dubos 1950,
p. 362). Second, Dubos observes, thé logical chain of
ideas was far more flexible than Pasteur granted. ‘His
career might have followed many other courses, each
one of them as logical, and as compatible with the
science of his time and with potentialities of his genius’’
(Dubos 1950, p. 377).

Dubos argues that Pasteur may have felt apologetic
both to himself and to his contemporaries and posterity
because he had failed to follow up his earliest ideas
on molecular dissymmetry with the vigor and skill he
brought to his other work. Perhaps this is why in the
1880's Pasteur implied so strongly that the chance

 
observation of the fermenting tartrate solution, rather
than the study of amyl alcohol and M. Bigo’s beet juice,
had carried him from crystallography to fermentation
research. The fermenting tartrate solution was so good
an example of the correlation of molecular dissymmetry
with the process of life that it should have been the link
in the logical chain of discovery. The studies of amyl
alcohol, let alone the industrial problems of beet juice
fermentation, were less direct, less reasonable, less
satisfying intermediate steps and therefore harder to
acknowledge.

There is yet another kind of “almost inflexible logic’
that governed Pasteur’s account of his work. To Pasteur,
as we have seen, it was axiomatic that ‘‘pure’’ science
preceded its applications. The very word “‘application”’
implied the pre-existence of pure science standing
ready to be used. Furthermore, within the intellectual
and scientific heritage of his time — a heritage that
persists today — Pasteur viewed pure science, the estab-
lishment of theory upon sound experimental studies of
natural phenomena, as a superior kind of activity; that
was how a scientist ought to spend his limited time and
energy. Consequently, Pasteur often ignored in his
autobiographical remarks the immediate practical

problems or motives that may have provided the occa-

sion for taking up a line of research. If we had to rely
entirely on Pasteur’s published scientific papers and
lectures we would never guess, for example, that the
lactic acid ferment research had begun with his visits
to a beet juice distillery. The logic of the relationship
between science and its applications demanded that this
commonplace problem could not be the starting point
for a major scientific discovery. Instead something else,
something that was unquestionably pure science, had to
come first. The puzzle of amyl alcohol’s peculiar optical
activity, even though it meant Pasteur had to admit to
working from preconceived ideas, was a more suitable
beginning than an industrialist’s request for help.

Once Pasteur had established the basic concept of
the microbial cause of fermentation, it was easier for
him to admit to working on practical questions: he
was simply using the theory to explain everyday ex-
amples of the general phenomenon. Even so, it is inter-
esting to see that he preferred to give only the most
impressive reasons for straying from the road of pure
science. He studied the diseases of wine, he says, partly
because the Emperor suggested it, partly because France
needed it. He apologized for undertaking the investiga-
tions on silkworm diseases: he was badly prepared for

it, he doubted he could carry it “to a logical conclu-
sion,’” he regretted abandoning the research on ferments
and spontaneous generation so dear to his heart. But,
again, it was a patriotic duty, and the Minister of Agri-
culture (he does not mention J. B. Dumas’ request)
had himself made the request (Lechevalier and Solo-
torovsky 1965, pp. 39-40). Nationalistic fervor also
inspired his last contribution to the problems of fermen-
tation. He had bitterly watched France's defeat in the
Franco-Prussian War of 1870 and resolved to prove to
the world that France could surpass Germany even at
the thing Germany did best: with processes derived from
the fecund principles of his research on wines, vinegars,
and silkworm disease, he declared, France could produce
a ‘beer of national revenge’’ superior to Germany's
finest brew.!?

We must, in short, be wary of accepting Pasteur’s
version of the origins, motivations, and character of his
research. His day-to-day correspondence and his labora-
tory notebooks provide more reliable evidence than his
published papers. In his papers he was all too likely to
make progress of his research appear to conform to his
notions of the way science ought to proceed: always
from theory to practice. No wonder his biographers
cannot agree whether he was primarily a pure scientist
distracted by practical concerns or a brilliant and lucky
applied scientist. Pasteur’s own historiography makes
it difficult now to say just which of his many contribu-
tions to biology and physiology and to medicine and
industry were the result of research directed toward
a problem of immediate human importance and which
were the result of research inspired by scientific curios-
ity. Both kinds of research certainly fed into his most
general scientific accomplishment, the founding of the
discipline of microbiology, although his spectacular
later achievements (joined to those of Robert Koch) in
research on disease gave the new science a decidedly
medical bent.

Nevertheless, the careful study of some of Pasteur’s
discoveries reveal where new insights into life processes
flowed from research on a practical problem. His patri-
otically inspired studies of beer, for instance, although
“based on the same principles’ as his studies of wine
and silkworm diseases, forced Pasteur to work out the
biology of yeasts and to formulate his general theory of
fermentation as ‘life without air.”” One particularly
noteworthy result of these studies, given the contempor-
ary debates on spontaneous generation and Darwin's
theory of evolution, was the demonstration that one

 
kind of microscopic mold could not turn spontaneously
into another, as Pasteur and many others had once
firmly believed (Duclaux 1920, pp. 193-197). Before
then, Pasteur’s studies of vinegar manufacture — espe-
cially his comparisons between the open barrel system
of the Orlean industry and the beechwood chip system
of the Germans — had yielded the information he
needed to disprove part of Liebig’s theory of fermenta-
tion.

The most important example, of course, is Pasteur’s
work on lactic and alcoholic fermentation in M. Bigo’s
beet juice distillery. His 1857 paper stated several funda-
mental new ideas in biology explicitly, and hinted at
others. He asserted that fermentations are caused by
microscopic living organisms; that fermentations are
correlated with the development and organization of
the tiny creatures, not with their death and decompo-
sition; that each kind of fermentation is due to a specific
kind of microorganism; and that each kind of micro-
organism needs a particular set of environmental condi-
tions for its growth and reproduction. He gave ingenious
methods for growing pure cultures of microorganisms,
the technical prerequisite for any successful microbio-
logical research. He commented on the specific dif-
ferences in the microbes’ vulnerability to changes in
their surroundings — the acidity of the medium or the
presence of an antiseptic like the oil of onion juice
(and how, one wonders, did Pasteur come to think
of trying onion juice?). He described the competition
between microorganisms for organic nutrients. And, he
implied that spontaneous generation was impossible,
that even germs had parents like themselves — a con-
clusion that modern geneticists see as ‘‘the axiomatic
foundation of molecular biology’ (M. R. Pollock, in
Monod and Borek 1971, p. 83; Handler 1970, p. 19).
But, above all, Pasteur made it plain that microorgan-
isms, until then little more than a curiosity of science,
played a literally vital role in the economy of nature —
not just in the economy of France.

 
Notes Chapter 2

1. See, for example, Pasteur’s “Note sur |’enseignement
professionel” (1863) and his “Porquoi la France n'a pas trouve
d’hommes supérieurs au moment du peril?” (1871), in Oeuvres
Vil, pp. 187-190, 211-221.

2. Pasteur’s meaning comes through most clearly in his
earliest and least epigrammatic expression of these views. In
1855 he wrote a letter about the receptivity of the distilleries
of Lille to science, and commented that they were handicapped
by their belief that there was applied science, that the applica-
tions make up a body of doctrine. In truth, of course, Pasteur
continued, the applications of science are only deductions from
purely scientific discoveries (Correspondence I, p. 382-383, to
the Rector of the Academie de Douai, 15 Nov. 1855). His bio-
graphers have relied on his later statements made in his 1863
note on professional education addressed to the Minister of
Public Instruction, Victor Duruy (Oeuvres VII, p. 188) and his
1871 article ‘Pourquoi la France n'a pas trouve d’hommes
supérieurs au moment du peril?’ (Oeuvres VII, p. 215). He
used the aphorism once again in a speech on the difference
between the taste of the grapes and the wine made from them
at the Congres viticole et sericole de Lyon in 1872 (Oeuvres
111, p. 464).

3. For materials on the status of and relationships between
science and technology in the 19th century see Merz 1965,
especially Vols. | and 11; Singer et al. 1958; and Taton 1965.

4. Among the significant early developments in crystallo-
graphy that formed a background to Pasteur’s early researches
was Malus’ 1808 discovery that all reflected light is polarized:
the vibrations of reflected light are not in all directions perpen-
dicular to the light ray, as in ordinary light, but are restricted
to one direction. The plane formed by the ray and its perpen-
dicular vibrations was called the plane of polarization. Then, in
1810, Hauy discovered small facets (or faces) on quartz crystals,
facets which could not be predicted from the normal form of
the crystal, a regular hexagonal prism bounded by two six-faced
pyramids. Hauy hypothesized that crystals are composed of
characteristic molecules arrayed in three-dimensional patterns,
a conviction shared by Pasteur. To others, the tiny facets in the
varied, complex, rough structures of crystals represented random
flaws, not characteristic variations of structure.

From observations of polarized light passed through quartz
crystals, Argo reached several conclusions in 1811, among them
that quartz crystals could split white polarized light into several
colored rays, which were deflected at different angles upon
leaving the quartz crystal. Then, in 1813 Biot gave lawful form
to these and many other physical phenomena of the deviation
of polarized light by quartz crystals. One observation, which
he studied with precise measurements, was that different quartz
crystals deviated polarized light sometimes to the right and
sometimes to the left. Finally, and importantly for Pasteur’s
later work, Biot discovered that certain solutions of organic
processes, one such solution being tartaric acid, deviated the
plane of polarized light. While inorganic crystals deviated polar-
ized light, inorganic solutions never did. The organic solutions
were unique. From these findings Biot concluded, though not
stated so precisely, that rotation of the plane of polarization of
light depended somehow on the crystal form of quartz, and on
the molecular form of organic solutions.

23

5. In 1819, Mitscherlich discovered that chemical com-
pounds having the same number of atoms, irrespective of the
nature of those atoms, took the same crystal form, a phenom-
enon termed isomorphism. Its definition was later modified to
state that compounds having the same number of atoms took
roughly similar crystal forms. Then Liebig, in 1824, was one of
several chemists who discovered that compounds having the
same elements in the same numerical proportions could have
entirely different qualities, a phenomenon named isomerism by
Berzelius in 1830.

Tartar was a by-product of the fermentation of grapes. In
1770 Scheele, using the double salt of potassium and sodium
tartrate, prepared the first organic acid, tartaric acid, which
found wide use in the textile industry and in medicine. Tartaric
acid’s remarkably similar cousin, racemic or paratartaric acid,
was discovered by Gay-Lussac in 1826, in crystalline form
mixed with crystals of ordinary tartaric acid during wine ferman-
tation. The study of isomerism began to preoccupy chemists
after Berzelius in 1830 found that the salts of tartaric and
racemic acid were chemically identical. He then asked Mitscher-
lich to study the crystals of these salts in hopes that “should
the forms be different, then the awkward difficulty of the dual
relationship of bodies with the same composition would be
solved in a simple and possibly correct manner’’ (Bernal 1953,
pp. 188-190). Biot communicated Mitscherlich’s results to the
French Academie in a note in 1844. It was Pasteur’s reading of
this note in 1846, when he was a student at the Ecole Normale,
that led him into his later famous studies of tartaric and racemic
acid.

6. It is not clear from published accounts whether Pasteur
(or the Bigos) believed that the round yeast-globules changed
shape as the fermentation changed from alcoholic to lactic acid,
or whether he realized that there were two kinds of globules
corresponding to the two kinds of fermentation and that the
longer globules were supplanting the round ones. In Pasteur’s
later work on silkworm diseases, he made recommendations to
the silkworm growers long before he understood the nature of
the disease. It is not impossible that he gave the Bigos a conven-
ient rule-of-thumb to follow before he knew that the different-
shaped globules were different kinds of living organisms.

7. The controversy over the nature of fermentation that
raged during the 19th century, involving such eminent figures
as Liebig, Berzelius, and Pasteur, was central to the debates
among chemists and biologists about the nature of the differ-
ences between inorganic and organic matter, and to the debates
between ‘‘vitalists’’ and ‘‘reductionists’’ about the nature of
living matter. For accounts of the fermentation controversy
see: Bulloch 1938, pp. 41-55; Conant 1952; Merz 1965, |: pp.
191-218 and II: pp. 106-117, 387-396; Farley and Geison 1974.

8. The date on which Pasteur observed this is in dispute.
Bulloch (1938, p. 60) gives 1858, the year Pasteur published his
““Memoire sur la fermentation de I'acide tartarique,’’ Oeuvres /1,
p. 24-28. Dubos (1950) says first 1854 (p. 41) and then 1857
(p. 106) without noticing the contradiction. R. Vallery-Radot
(1919) gives no date but suggests by his narrative that the inci-
dent occurred in 1854. P. Vallery-Radot (Oeuvres /1, p. vi) gives
27 August 1857 as the date on which ‘‘Pasteur set in motion the
experiment which showed that, when ammonia racemate started
 

fermenting, the left-handed tartrate appeared and the right-
handed tartrate decomposed.” However, in his “The Story of
Pasteur’s Discovery’ (19579), he suggests that Pasteur had made
the observation before he published the 1857 lactic acid fermen-
tation paper, but did not work on it until afterwards. The first
mention of the observation in Pasteur’s correspondence is in a
letter to his mentor, the celebrated old chemist, J. B. Biot, 7
September 1857 (Correspondence Il, pp 427-428 and notes)
which makes the 27 August 1857 date most plausible.

.

9. On the discovery of the ‘Pasteur effect,” see Lechevalier
and Solotorovsky 1965, pp. 23-29; Pasteur, ‘Sur la fermentation
visqueuse et la fermentation butyrique,’” 1861, Oeuvres II,
pp. 134-135; and “‘Faits nouveaux pour servir a la connaissance
de la théorie des fermentations proprement dites,”” 1872, Oeu-
vres 11, pp. 387-394.

10. In this very brief account of the Pasteur-Pouchet debate,
we have had to leave aside several important scientific and
political issues. Emile Duclaux (1920, pp. 109-111), Pasteur’s
student and collaborator, pointed out that, if Pouchet had not
withdrawn, Pasteur would have found it hard to explain away
Pouchet’s experiments with hay broth: the spores of the hay
bacillus readily withstood the preliminary boiling of the broth,
and the subsequent growth of the bacillus looked very much like
spontaneous generation.

Farley and Geison (1974) have shown that the French
scientific establishment found Pasteur’s disproof of spontaneous
generation congenial on religious and political grounds. The
commission itself, they note, was strongly biased in Pasteur’s
favor from the start; two members, for example, were teachers
and close friends of Pasteur and one (Balard) had even suggested
the use of swan-neck flasks for the experiments in spontaneous
generation!

11. Liebig died in 1873, still believing that fermentation in
general was a process of decomposition and that vinegar was
produced by a catalysis caused by the beechwood chips.

12. See Oeuvres V, p. 5, and Geison 1974, p. 354. For a criti-
cal evaluation of the practical results of Pasteur’s research on
beer, see Klécher 1903, pp. 4-6, 9, 353.
Chapter 2
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26
CHAPTER 3
BERIBERI AND THE COENZYME FUNCTION OF VITAMIN B,

The bacteriological triumphs of Louis Pasteur,
Rudolph Koch, and their followers so caught the imagi-
nation of scientists and doctors in the last two decades
of the nineteenth century and early years of the twenti-
eth century that it was almost impossible to imagine a
disease caused by anything but microbes or poisons.
Medical research was primarily directed at the difficult
but immensely satisfying tasks of tracking down the
micro-organisms responsible for a variety of infectious
diseases, isolating microbial toxins, and preparing vac-
cines and antitoxins. In 1890, when the Dutch govern-
ment commissioned a team of physicians to investigate
a disease which had begun to devastate the Dutch East
Indian colonies about twenty years earlier, everyone
fully expected to find a bacterium or parasite or, just
possibly, some kind of poison. The slow realization that
the disease, beriberi, was not caused by some tiny
organism or a potent toxin, but rather by the /ack of
minute quantities of an unknown and indispensable
nutrient in the diet, required a major shift in medical
and biological thinking. Over the first four decades of
this century, research on beriberi and on vitamin B;
(thiamine)!, both exemplified and helped to bring
about remarkable changes in our assumptions about
disease, nutrition, and the intimate workings of the
living cell.

The number of vitamins, the variety of their physio-
logical effects, and their confusing propensity for ap-
pearing in combinations make the history of their dis-
covery a long and complicated story. R. R. Williams,
who synthesized thiamine in 1936 and who then wrote
the first book devoted to a single vitamin, used as a
frontispiece to Vitamin B, (Thiamin) and Its Use in
Medicine a thick cable: each separate strand represented
one of the various components of the vitamin B; com-
plex as they had been laboriously unraveled by medical,
physiological, and chemical research between 1897 and
1938.

In this chapter we will trace only one of these strands,
that involved with the discovery and identification of
vitamin B; and then with the elucidation of its bio-
chemical role, as a coenzyme which functions in the
metabolic breakdown of sugars.

Disease, Biochemistry, and Nutrition: 1900

Many physicians reacted with scorn when Pasteur
promulgated the germ theory of infectious disease in the
1860's and 70's, but by the last decade of the nineteenth
century the medical profession had largely adopted the
new ideas. By 1900, when microbiology was a well-
established discipline, biochemistry was just beginning
to emerge as a field. The word itself had hardly been
invented, and the first journals, societies, university
departments, and classes in biological chemistry or
biochemistry were founded only in the first decade of
the twentieth century.

Biochemistry’s most obvious progenitor was physio-
logical chemistry, but the problems that the new science
addressed were in some ways more general than those
of physiological chemistry — as the bijo prefix implied —
and in other ways much more specific. In particular, the
mixed crew of physiological and organic chemists,
medical researchers, pathologists, bacteriologists, and
physiologists who came to call themselves biochemists
paid special attention to the chemical processes that
occurred within the living cell. The development of the
new field was given impetus by several discoveries in the
1890's which suggested that cells produce catalysts
which perform the chemical reactions of oxidation, fer-
mentation, respiration, and synthesis inside the cell.
Catalysts, or enzymes, which could start or accelerate
the breakdown of compounds outside the cell had long
been known, but in 1897 scientists first learned that the
enzyme of fermentation, zymase, could be extracted
from ground-up cells and used to ferment sugars. This
discovery, which earned Edward Buchner one of the
earliest Nobel Prizes in Chemistry in 1907, showed that
the chemical components of the cell could be studied
piece-meal, that the cell was not a single structural unit
which would lose all its physiological properties the
moment its membrane was broken (Kohler 1970,
pp. 162-178; Kohler 1971, pp. 35-61; Kohler 1973,
pp. 181-196).

The two major problems that the new science of
biochemistry set out to solve were the chemical struc-
ture and role of enzymes, and the chemical properties

 
 

of protoplasm. The cell was commonly viewed as a bag
of protoplasm and protoplasm was believed to be a
colloidal, jelly-like chemical compound of immense size
and complexity, and of such fragility that it had to be
studied intact. This mysterious substance somehow
absorbed and incorporated nutrients, synthesized all
manner of products, respired and fermented, grew and
reproduced. Biologists and chemists were daunted by
protoplasm, and any attempt to analyze it was consid-
ered foolhardy by many.

However, Buchner’s extraction of zymase as well as
the work being done on toxins and antitoxins suggested
to biochemists that at least some of the cell's chemical
components did have what was then understood to be
molecular structure. These compounds and the reactions
in which they participated could be studied in cell
extracts in the test tube. However, the difficulties that
early biochemists faced were tremendous. Their extracts
were crude; methods of extracting cell consitutents were
harsh; techniques for analyzing the extracts were ardu-
ous and time-consuming. Even the basic chemical nature
of enzymes was a matter of great debate, for many
biologists and chemists did not believe that enzymes
were proteins even after James Sumner in 1926 purified
and crystallized the enzyme urease, and showed that it
was a protein (Fruton 1972, p. 156 ff).

The first generation of biochemists spent little time
studying nutrition on the cellular and intracellular level,
although for at least a quarter of a century nutrition had
been one field where physiology and organic chemistry
had come together. In the late nineteenth century,
research in nutrition had followed two main lines:
determining the energy values of foodstuffs, and trying
to devise the physiologically and economically optimal
balance of ‘the nutritional trinity’’ of protein, carbohy-
drate, and fat (Armsby 1906, quoted in McCollum 1957,
p. 153; Ihde and Becker 1971, pp. 20-26). To early
twentieth-century nutrition researchers, the measure-
ments of human energy needs and of the caloric content
of foods were extremely impressive, because they
provided strong quantitative data that seemed to demon-
strate a ‘‘real measure of nutritional needs, independent
of, and apparently superior to, considerations based
upon chemical details (Hopkins 1929, pp. 211, 216). In
contrast, analysis of the proportions of the elements in
different foodstuffs to obtain a ‘‘proximate analysis’
of their protein, carbohydrate, fat, mineral, and fiber
content seemed to be leading nowhere, although over

28

3,000 samples of American foods and animal fodders
had been analyzed by 1890 (McCollum 1957, pp. 152-
55; Ihde and Becker 1971, pp. 20-26).

Both kinds of nutritional research ignored a point
which was becoming more and more obvious in practical
animal feeding experiments: the theoretical categories
of nutrient re too poorly defined to be useful. Even
research Wes which were obviously chemically
distinct and comparatively easy to study, was hampered
by assumptions about the nature of life and protoplasm.
Bunge, whose students turned out so many papers on
mineral nutrients, firmly believed that animals could
only use the more complicated organic mineral com-
pounds produced by plants. Bunge's view followed from
the general feeling that animal protoplasm was chemi-
cally so complicated and unique a substance that it
could only make use of organic substances like itself.
This assumption made Bunge ignore the implications
of work done by two of his students, Lunin and Socin,
who came close to proving the existence of unknown
nutrients later named vitamins — simply because the
synthetic diets Lunin and Socin had tried on mice
included inorganic salts rather than the vital organic
compounds (Hopkins 1929, pp. 213-214).

Beriberi, Chickens, and Rice

The disease beriberi has long been known in the Far
East, for there is a Chinese record of a beriberi epidemic
dating from 2697 BC (Williams and Spies 1938, p. 17).
In the early seventeenth century, a Dutch physician,
Jacobus Bontius, described the symptoms of beriberi
which he had observed in himself and his patients in
Java, and a similar disease named ship beriberi had
been known to attack Western sailors on long voyages
(Bontius 1642, pp. xxi-xxiii, 106, 111). In the latter half
of the nineteenth century, beriberi became a major
public health problem in Asia. It became endemic in
many countries, and was especially apt to devastate
groups of people who were compelled to live, sleep, eat,
and work together, such as prisoners, sailors, hospital
and lunatic asylum patients, and mothers and their
infants. In any of the forms it took, beriberi was a
ravaging disease. Some victims suffered from acute
burning sensations on the skins of their feet and from
grave weakness or paralysis in the legs as they wasted
away to mere skeletons. For others, the emaciation and
muscular atrophy was disguised by the swellings of
edema. Still others, babies especially, died suddenly of
acute heart failure. Many patients suffered all the vari-
ous manifestations in succession, and all too often the
disease was fatal.

The military were particularly alarmed by the ravages
of beriberi in army camps and on navy vessels. A young
medical officer in the Japanese navy, K. Takaki, heard
from his father how beriberi had killed many men of
the Imperial Palace Guard in 1862, and in his own
work at the Naval Hospital, Takaki sometimes found as
many as three-quarters of the patients ill with beriberi.
“Such conditions,” Takaki wrote in 1906 when he
explained why he had devoted so much of his life to
the study and eradication of beriberi, ‘used to strike
my heart cold when | came to think of the future of
our Empire, because if such a state of health went on
without discovering the cause and treatment of beriberi,
our navy would be of no use in time of need’ (Takaki
1906, p. 1369; Williams 1961, pp. 19-25; Harris 1938,
pp. 52-56). Takaki’'s fears were shared by the Dutch
colonial authorities in Indonesia — who were losing so
many soldiers to beriberi that they could not win a
guerilla war against Sumatran rebels — and by the
American colonial authorities in the Phillipines — who
watched helplessly as a tenth of the native police force
came down with beriberi every year (Jansen 1956,
p. 260; Williams 1961, p. 4). For such reasons, govern-
ments thought it important to find out what caused
and what might cure beriberi.

Since the disease obviously seemed to be contagious,
its cause was assumed to be a micro-organism. The first
task thus was to isolate the bacterium responsible, and
Takaki spent five years (1875-1880) in England learning
bacteriology for this purpose alone. The starting point
for the ultimately successful Dutch investigation also
was bacteriological. In 1886 the Dutch government
appointed a pathologist, Pekelharing, and a neurologist,
Winkler, as a commission to study the destruction of
the peripheral nervous system by beriberi and to search
for the infectious agent. Before going to Java, Pekelhar-
ing and Winkler stopped in Berlin to visit Koch's lab
and learn about the latest developments in bacteriology.
There they met Christian Eijkman, a young Dutch
doctor on leave from the Dutch East Indies colonjal
army, who asked to join the commission as an assistant.
In the colonies, the commission soon believed they had
found a coccus in beriberi patients which could not be
found in healthy people. Although they published this
conclusion, Pekelharing still had doubts as to whether
they really had isolated the bacterial cause of beriberi.

29

A young medical officer, J. van Eecke, who worked
closely with the commission and did bacteriological
research on his own, put it very bluntly: “Whether
the micro-organism we found is the pathogen or not is
a question that must be settled unequivocally. The short
history of bacteriology is already over-rich in examples
of premature conclusions’ (van Eecke 1887, p. 85).

To decide the question according to the rigorous
canons of bacteriology he had learned from Koch,
Eijkman remained in Djarkarta as a civilian medical
researcher after Pekelharing and Winkler went home to
the Netherlands in 1888. Eijkman began by trying to
give animals beriberi, inoculating them with infectious
matter from beriberi patients in the hospital. For his
experimental animals, he made a somewhat unorthodox
but fortunate choice. He used chickens, probably be-
cause they were cheap, easy to obtain, and easy to care
for, but also perhaps because he had heard that, during
an outbreak of beriberi in the Moluccas, large numbers
of the birds and hens had also suffered from the disease
(Jansen 1959, pp. 70, 74). The bewildering variety of
forms that beriberi took presented Eijkman with a
problem: how would he know if his hens had caught
beriberi? He decided to look for evidence of degenera-
tion of the peripheral nerves (polyneuritis), a prominent
and painful symptom of human beriberi. But for several
months the hens showed no signs of anything resembling
beriberi (Jansen 1956, pp. 260-65).

Like Pasteur, however, Eijkman was prepared to take
advantage of accidents and ‘’chance’’ observations. One
day in 1889 he found his chickens sick with something
that closely resembled beriberi. The signs of polyneuritis
were especially plain: the unhappy birds staggered and
collapsed, their wings drooped in partial paralysis, their
heads and necks were pulled sharply backwards by
peculiar muscular spasms. But it seemed unlikely that
the inoculations were responsible, for the inoculated
chickens and the uninoculated controls were equally
sick and nearly three-fourths of each flock died. When
Eijkman examined the dead birds, he found that both
groups showed the distinctive signs of nerve degenera-
tion that he knew so well from his microscopic studies
of nerves from beriberi victims. Six months later, the
few birds who survived what Eijkman cautiously called
polyneuritis gallinarum  (polyneuritis of chickens)
recovered quite suddenly and did not relapse.

On investigating the sudden outbreak of polyneuritis
and its equally sudden and mysterious disappearance,
Eijkman discovered that the chickens’ diet had been

 
changed twice. When he began his unsuccessful inocula-
tions, the birds were being fed crude unmilled rice.
Then the servant in charge of feeding them begged table
scraps of polished white rice from the hospital; after
a few weeks of eating this rice, the birds fell ill. Later,
when a new hospital cook “refused to allow military
rice to be taken for civilian chickens,” their feed again
consisted of the crude, unpolished rice (Eijkman 1929,
p. 203). Soon afterwards the chickens got well and
stayed healthy. Moreover, sick birds recovered when
they were fed the rice polishings and rice germ. Clearly,
something about the white rice caused polyneuritis
gallinarum, and something in the red skin and germ
of the unmilled rice prevented and cured the disease.

Eijkman’s “lucky accident” and his simple test of
his observation gave him a new freedom in his work on
beriberi, for he could now produce the disease at will
in his experimental animals. This still left him open,
however, to the criticism that chicken polyneuritis was
not the same disease as human beriberi, a problem
that was met when Eijkman took advantage of a ‘’natu-
ral experiment’’ with Javanese prisoners. He asked the
medical inspector of the prison system to collect infor-
mation about the incidence of beriberi in the island's
jails and about the kinds of rice their 300,000 prisoners
ate. The inquiry revealed that in jails where prisoners
milled their own rice by hand according to their local
custom, the inmates came down with beriberi at only
1/300th the rate found in jails where prisoners were
given industrially milled polished white rice. Indeed,
all but one of the 37 jails where prisoners prepared their
own rice were completely free from beriberi (Eijkman
1929, pp. 205-206). To Eijkman, although not to the
prison authorities or other experts in tropical medicine,
the results seemed unequivocal.

When Eijkman tried to explain why polished rice
should be so dangerous and unmilled rice with its germ
and skin intact should be so beneficial, he fell back on
the prevailing assumptions of bacteriology. If the cause
of a disease was not a micro-organism, he reasoned,
then there must be a toxin which was neutralized by
something in the red skin and germ. Eijkman continued
to believe for many years that the starchy white grain
contained an active toxic substance, a belief strength-
ened by his showing in 1896 that beriberi was not
caused by a dietary protein deficiency.?

In 1896 Gerrit Grijns, a young surgeon who had
served periodically as Eijkman’s assistant since 1893,

30

succeeded Eijkman as director of the Djarkarta labora-
tory. The Dutch East Indies government asked Grijns
to “investigate the physiological and pharmacological
properties of the tannin contained in red rice, and
possibly other constituents of this kind of rice which
might require consideration in relation particularly to
beriberi’’ (Grijns 1935, p. 1). He was assured that he
should not restrict his research to this problem, but
instead should extend Eijkman’s results to discover
more about the connection between diet and polyneu-
ritis and about the anti-beriberi properties of red rice.

Grijins continued the work on chicken polyneuritis,
first by finishing Eijkman’s incomplete experiments on
“’salt-starvation’’ as a possible explanation for the harm-
ful white rice diet. Over the next four years, he im-
proved Eijkman’s experimental techniques, and he
explored many ideas. Did the origin of the rice make
a difference? Was the loss of fats contained in the rice
skin significant? Was the starch of rice, sago, and
tapioca really positively harmful, as Eijkman had con-
cluded in his 1895 and 1896 reports? What was the
active substance in rice skin? Could other foods cure
beriberi as effectively as rice skin and rice germ?

In casting about for other foods that prevented or
cured beriberi, Grijns happened on a kind of pea, Phase-
olus radiatus (Katjang idjoe in Malayan), which was
often used in Java to supplement chicken-feed. The
results of tests with this kind of pea in birds who were so
ill with beriberi that they had to be fed by hand were
striking; within three or four days they could feed them-
selves, and within ten days they could walk easily again.
Both the skin and kernel of the pea were equally effica-
cious, but the peas lost their curative and preventive
powers when cooked in steam at 120°C. The discovery
of the peas’ effectiveness led to a series of experiments
which neatly disproved Eijkman’s theory of toxins
produced by starches, by showing that polyneuritis
could be produced in pigeons and fowl with a diet that
contained no starch or carbohydrate at all.

Grijns’ report in 1901 on his five years of work with
nearly two hundred fifty birds began by recapitulating
and arguing against theories of a bacterial or toxic cause
of beriberi. At the same time, he stressed that his work
strengthened Eijkman’s important finding that chicken
polyneuritis and human beriberi were the same. He
concluded with the first clear statement of the existence
of previously unknown ‘protective substances’ whose
absence from the diet led to ‘partial starvation.”
 

There occur in various natural foods, substances,
which cannot be absent without serious injury
to the peripheral nervous system. The distribution
of these substances in the different food-stuffs is
very unequal. Of those examined, phaseolus radi-
atus and cajanus indicus were the richest, and
polished rice the poorest, in these substances.
The separation of these substances meets with
the difficulty that they are so easily disintegrated.
This disintegration, which takes place in a damp,
warm place, shows that they are very complex
substances. They cannot be replaced by simple
chemical compounds (Grijns 1935, p. 38).

To judge by the dates of Grijns’ various experiments,
he had had serious doubts about Eijkman’s toxin theory
within a year of starting his research, and he probably
hypothesized the existence and distribution of the
protective substance early in 1898. His experiments
between 1898 and 1901, designed to clear up details
about the chemical constituents of substitues for rice
skin and the rice skin itself, were founded on Grijns’
belief that a new vital dietary substance was involved.

Grijns’ first paper had little effect when it was pub-
lished in 1901. Both Eijkman and he published their
results in the medical journal of the Dutch East Indies
and summarized them in the leading medical journal
of the Netherlands; but their articles were in Dutch,
which severely limited their audience. Moreover, as
late as 1906 Eijkman was still hesitant about accepting
Grijns’ “partial starvation’’ theory, for he would not
discard his own toxin hypothesis until he had repeated
all the experiments on potato starch and peas (Eijkman
1906, pp. 156-58). (It thus is interesting to see how
carefully Eijkman avoided discussing his long-held
toxin and antidote theory in his 1929 Nobel Prize
lecture; he only spoke about the “‘anti-neuritic prin-
ciple” of the rice skin, not at all about the poisons in
the starchy grain! ) Only two Norwegian researchers,
Holst and Frolich, who were studying ship beriberi,
tried to follow up Eijkman’s and Grijns’ research imme-
diately. Believing that tests on mammals would be
more instructive than tests on birds for explaining hu-
man pathology, they chose the guinea pig as their
experimental animal. Their results were unexpected;
they were able to produce scurvy, but not beriberi,
and switched their research to take advantage of this
finding (Holst 1907, pp. 619-633).

Although little attention was paid to Eijkman’s and
Grijns’ work at the time, the problem of beriberi was
not being ignored. During the first decade of the 20th
century, several other physicians in Asia arrived more or
less independently at the connection between a diet
of polished rice and beriberi, and provided valuable
new evidence for what would become the vitamin theory.
Braddon, an English doctor, observed striking differ-
ences among four cultures living in Malaya in regard
to their use of rice and their incidence of beriberi. The
Malays who milled their rice at home by hand, the
Tamils who parboiled their rice before removing the
rice skin, and the Europeans who did not eat rice were
all free from beriberi, but the Chinese who ate imported
rice suffered severely from the disease. Braddon believed
that a toxin, perhaps from a saprophyte, formed in
white rice as it grew stale. His theory was tested by
Fletcher on patients in a lunatic asylum, where nearly
half the patients had beriberi and a quarter of those
died of it. He confirmed the relationship between the
rice diet and the disease, but left the explanation open.

In 1907, Fraser and Stanton tried different kinds of
rice diets on Javanese laborers who were building roads
in isolated areas of Malaya. After finding that a white
rice diet did indeed produce beriberi, they tried some-
thing that, rather surprisingly, Eijkman and Grijns had
not done: they tried to extract the hypothetical toxins
from white rice. In addition, they showed that if an
alcoholic extract were made of parboiled rice, the rice
after extraction was no longer any better than milled
white rice. But the extract could be fed along with
polished rice and prevent the beriberi that the polished
rice diet would usually cause. Fraser and Stanton con-
cluded that the polished white rice lacked ‘“‘some sub-
stance or substances essential for the normal metabolism
of nerve tissues’’ — a clear statement of the deficiency
theory (Williams 1961, pp. 43-49). Fraser and Stanton
presented their work at the first meeting of the Far
Eastern Association of Tropical Medicine in 1910,
at which time the association resolved that: “‘sufficient
evidence has been produced in support of the view
that beriberi is associated with the continuous consump-
tion of white (polished) rice as the staple article of diet,
and the Association accordingly desires to bring this
matter to the notice of the various governments con-
cerned’’ (Williams 1961, pp. 48-49).

Fraser and Stanton’s report was heard by an Ameri-
can, Vedder, who also knew of Eijkman’s and Grijns’

 
work. Vedder enthusiastically adopted Fraser and
Stanton’s deficiency theory because he had already
seen that Grijns’ results implied a kind of nutritional
deficiency that was simpler and more fundamental
than that implied by Grijns’ phrase “‘protective sub-
stances.” To help him find out exactly what the essential
substances in extracts of rice skin or parboiled rice
were, Vedder recruited a young chemist at the Manila
Bureau of Science, R. R. Williams. Vedder's enthusiasm
was contagious, and for years Williams worked in his
spare time until he at last succeeded in isolating and
synthesizing the active anti-beriberi principle (Williams
1961, pp. 1, 48-50, 95 ff).

Rats, Milk, and Minimal Diets

While physicians in Asia were proving a strong con-
nection between disease and diet and formulating the
new theory of nutritional deficiencies of unknown
substances, a different kind of research in the United
States and England yielded other important evidence
of the need for accessory food factors. For these work-
ers, the impetus for undertaking such research did not
come out of a desire to understand a particular disease,
although several of them did have practical applications
in view. They hoped to determine the simplest diet
for farm animals and experimental animals and to use
that knowledge as the basis for further nutritional
experimentation. By 1906, there were already about a
dozen papers scattered throughout the literature and
published in at least four different languages, which
described chemically simplified or synthetic diets. As
a rule, the authors of these papers knew little, if any-
thing, about one another's work, and very often they
did not follow up on their own observations. Looking
back, we can see that they were on the right track, but
they had no way of being sure at the time.

The great French chemist, Dumas, for example,
attempted to invent a substitute for mother’s milk
during the siege of Paris in 1870. The disastrous effects
of his mixtures of emulsified fat and sweetened protein
— in theory a complete food — led him to conclude
that a vitally important ingredient was lacking, but
Dumas did not try to identify the differences between
real milk and his artificial concoction. The work by
Lunin in 1880 and Socin in 1891 on inorganic minerals
and salts in the diet also suggested that milk and egg
yolks contain more than just the basic protein, fat,
carbohydrate, and minerals. They used very small
numbers of experimental animals, so their results were

32

not conclusive; and their professor, Bunge, as we have
mentioned, discouraged them on theoretical grounds
from continuing (Ihde and Becker 1971, pp. 11-12).
Ironically, the one scientist who did take Lunin and
Socin’s work seriously was C. A. Pekelharing, the Dutch
pathologist who had sought a bacterial cause of beriberi
in 1888. In 1905 he published the results of several
years of research which demonstrated the existence of
“an unknown substance in milk which even in very
small quantities is of paramount importance to nourish-
ment. If this substance is absent, the organism loses its
power to assimilate the well-known principal parts of
food. . .Undoubtedly this substance not only occurs in
milk, but in all sorts of food stuffs both of vegetable
and animal origin’’ (Pekelharing 1905, p. 122).

In Great Britain the most important work on sim-
plified diets at the beginning of the twentieth century
was done by Frederick Gowland Hopkins, one of the
most influential figures in the history of vitamin research
and biochemistry. As a young man, Hopkins trained
for a career as an ‘‘analyst,”” which then meant a pro-
fessional analytic chemist. At the age of 28, he decided
to study medicine and as a medical student began doing
valuable research in physiological chemistry and pathol-
ogy. As he recalled in his 1929 Nobel Prize address, how-
ever, his clinical work excited an interest in nutrition:

Early in my career | became convinced that cur-
rent teaching concerning nutrition was inadequate,
and while still a student in hospital in the earlier
eighteen nineties | made up my mind that the
part played by nutritional errors in the causation
of disease was underrated. The current treatment
of scurvy and rickets seemed to me to ignore the
significance of the old recorded observations.
| had then a great ambition to study those diseases
from a nutritional standpoint (Hopkins 1929, p.
217).

Rather than going into clinical medicine, Hopkins took
up an unexpected offer in 1898 to ‘‘develop. . .teaching
and research in the chemical side of physiology’ at
Cambridge (Needham and Baldwin 1949, p. 20). Sixteen
years later, the university founded a chair of biochemis-
try, appointed Hopkins the first professor, and put him
in charge of the new department of biochemistry.
Hopkins’ research in his first years at Cambridge
concentrated on proteins and amino acids. “‘l realized,”
he said in 1929, “‘as did many others at the last century's
close, that for a full understanding of so many other

 
aspects of biochemistry, further knowledge of proteins
was then a prerequisite; and. . .I did my best to contrib-
ute to that knowledge’’ (Hopkins 1929, p. 217). By
capitalizing on his discovery of an impurity in acetic
acid while teaching a laboratory session on proteins,
Hopkins was able to isolate and identify tryptophane,
an amino acid whose existence had only been postu-
lated before then. Hopkins followed this achievement
by showing that the protein of maize, zein, lacked this
amino acid. More important still, he found that an
artificial diet which contained adequate amounts of fats,
carbohydrates, and minerals with zein as the only
protein, could not keep mice alive; as soon as trypto-
phane was added to supplement the zein, the mice
survived much longer.

Hopkins realized clearly and quite early in his work
on proteins that a variety of nutrients were required for
health and life. In an interesting speech to the Society
of Public Analysts in 1906, ‘The Analyst and the
Medical Man,” Hopkins stressed that:

No animal can live upon a mixture of pure protein,
fat, and carbohydrate, and even when the neces-
sary inorganic material is carefully supplied the
animal still cannot flourish. The animal body is
adjusted to live either upon plant tissues or on the
tissues of other animals, and these contain count-
less substances other than the proteins, carbohy-
drates, and fats. Physiological evolution, | believe,
has made some of these well-nigh as essential as
are the basal constituents of diet.

He cited lecithin as one such substance that was already
known, and pointed to rickets and scurvy as diseases
in which empirical dietary cures had been found long
ago. These illnesses and other less obvious or severe
“nutritive errors’’ were, Hopkins insisted, certainly due
to “minimal quantitative factors’ in the diet. He asked
the analytic chemists to help the doctors by identifying
and isolating these “unknown substances with unknown
properties, present in complex mixtures.” His audience's
response to this appeal was disappointing; only one
chemist addressed himself to the question of diet and
disease, and then simply to point how impossible diffi-
cult, expensive, and time-consuming such analysis of
foodstuffs would be (Hopkins 1906, pp. 394-96, 401).

At the time of this speech, Hopkins had been using
simplified diets to test the qualitative effects of different
proteins and amino acids on the growth of young rats.
Although the addition of tryptophane to zein length-

ened survival time, the rats still did not grow properly.
By substituting casein (milk protein) for zein, by adding
a small quantity of milk to the simplified diet, or by
using yeast extracts to make the dull, tasteless diet more
appetizing, he could bring the young rats’ growth
patterns back to normal. From 1906 to 1912 Hopkins
tried to understand how these small changes in the
diet could make so great a difference in the rats’ growth.
For a number of reasons, however, he published nothing
and only gave a couple of talks on his experiments
before 1912 (Hopkins 1929, p. 218; Dale 1948, pp.
130-131).3

While Hopkins moved from studies of the nutritive
values of different proteins to the inadequacies of
synthetic diets, American researchers at the Wisconsin
and Connecticut agricultural stations undertook similar
research. Like Hopkins, they began with the assumption
that all proteins do not possess equal food value. At the
Connecticut Agricultural Experiment Station in New
Haven, Thomas Osborne began preparing pure vegetable
proteins and analyzying their amino acid content from
the 1890's on. A young chemist from Kansas, Elmer V.
McCollum, came to Yale in 1904 to do graduate work in
organic chemistry. He specialized in physiological
chemistry, took courses on nutrition from Lafayette
Mendel and Russell Chittenden, the leading American
authorities, and worked on amino acid determinations
at Osborne's laboratory. McCollum recalled hearing
Mendel lecture on Hopkins’ work on supplementing
zein with tryptophane in 1906-07; he also remembered
that none of his teachers ever mentioned beriberi,
scurvy, rickets, or pellagra (McCollum 1953, p. 301).

In 1907, while Osborne and Mendel proceeded with
tests of the nutritive values of their purified proteins,
McCollum went to the University of Wisconsin's College
of Agriculture and Research Station to perform chemical
analysis of cattle feeds. McCollum did a thorough search
of the literature on animal nutrition and collec =d
accounts of other attempts to restrict diets in order tc
determine the requirements for particular substances.
He was ‘‘astonished to find that every effort which
had been made to feed animals on such mixtures (of
isolated proteins, carbohydrates, fats, and mineral-salt
mixtures) had resulted in prompt failure of their health,”
and he realized then ‘‘that the most important discovery
to be made in nutrition would be the elucidation of the
cause or causes of these failures” (McCollum 1953,
pp. 304-05).

For a number of reasons, .he cattle-feeding experi-

 
ments that McCollum was to conduct proved impracti-
cal. And so, in 1907, he set up the first rat colony in
America for nutritional studies. McCollum kept in touch
with his Yale professors and in 1909 Mendel and Os-
borne also began using rats as experimental animals for
their protein tests.

Like Hopkins, McCollum worried about the palata-
bility of the insipid simplified diets he used on his rats,
and tried to add flavor and variety to their diet. In so
doing, he unwittingly saved his rats from vitamin defi-
ciencies by allowing them to eat whey-contaminated
lactose and their own feces — both sources of vitamins
not otherwise provided by the simplified diet. In a
1913 paper, McCollum and his co-worker, Margaret
Davis, showed that fats, or something associated with
fats, extracted by ether from butter or egg yolks, con-
tained something necessary to the growth of young
rats. As long as the diet consisted of casein, carbohy-
drates, salt, and lard, they were able to keep the rats
alive and growing for a few weeks, after which the rats
did not gain any more weight. But the addition of
ether-extracts of butter or yolk to the diet at this point
would set the rats growing rapidly (McCollum and
Davis 1913).

Meanwhile, at the Connecticut research station,
Osborne and Mendel had been working along similar
lines; establishing a basic diet of ‘protein-free (skim)
milk,” carbohydrates, salts, and lard, and then testing
the effects of different proteins. But until 1912 they
were unable to get rats to grow full size on their basic
diet (Osborne and Mendel 1911, pp. 618-698). Then,
in desperation, they reconsidered every constituent of
milk, realized that all their milk substitutes and diets
lacked the cream of milk, and tried replacing lard with
butterfat. The results were so immediately successful
that they began to write up the new experiments for
publication (Osborne and Mendel 1913a, b). To their
chagrin, however, their rivals McCollum and Davis won
what had been a conscious race between the Connecticut
and Wisconsin researchers. In the summer of 1913
Osborne wrote to Mendel, ‘I have just received the
July issue of the Journal of Biological Chemistry and
notice McCollum’s article in it, which | assume you
have seen. If not, | might say that he could just as well
have taken his data from our notebooks as from his’’
(Becker 1970, p. 158-59).

The “*Vitamine” Theory: 1911-1920

Hopkins, McCollum and Davis, and Osborne and
Mendel gave a new direction to nutritional studies ty

34

their agreement that complete growth required the food
factor in milk, by their demonstration of the value of
rats as experimental animals, and by their use of growth
rate as the measure of dietary deficiency. But much of
the force of their papers came from their explicit recog-
nition that their work and the research on beriberi and
scurvy were closely allied. For this idea, they were
indebted in some measure to Casimir Funk, a young
Polish chemist working in England, who had begun to
study the beriberi-preventing substance in rice skin and
yeast in 1911. Funk's review of the literature, his bold
speculations about the nature of deficiency diseases,
and his invention of the word ‘vitamine’’ as a name
for the mysterious food factors implicated in deficiency
diseases, all argued that there was an underlying unity
to the diverse studies of beriberi, scurvy, and the growth-
promoting factor in milk. In effect, Funk did what
Hopkins had failed to do with the insights so clearly
expressed in the 1906 speech to the analysts: he pro-
vided a theory of nutrition and disease that was as
dramatic and as amenable to scientific verification as
Pasteur’s germ theory of infectious disease. From 1912,
when the new word first appeared in print, to the
1940's, vitamin research was as exciting a field as bac-
teriology had been in the late nineteenth and early
twentieth century.

After receiving his Ph.D. in organic chemistry in
1904, and then studying under the noted biochemist,
Gabriel Bertrand, at the Institut Pasteur in Paris, Funk
did research on amino acids and proteins in synthetic
diets for dogs with the physiological chemist, Abderhal-
den. In 1910, an English friend in Abderhalden’s labora-
tory found Funk a job at the Lister Institute in London,
where his attention was soon directed to the problem
of beriberi (Harrow 1955, pp. 35-39).

C. J. Martin, the first director of the Lister Institute
of Preventive Medicine, was interested in tropical dis-
eases and encouraged his friend Braddon's work on
beriberi in Malaya. Martin also was a close friend of
Hopkins, and knowing Hopkins’ research on trypto-
phane deficiency in zein, Martin guessed that the cause
of beriberi might be some other sort of amino acid
deficiency in polished rice (Chick 1956, pp. 134-39,
197-98). Since Funk had experience with amino acid
determinations, Martin suggested that he analyze the
amino acid content of the rice and rice skins Braddon
had sent to the Institute (Harrow 1955, p. 39). At the
time, Martin's amino acid hypothesis was as plausible
as any other theory about beriberi — and there were a
good many. Although there was considerable agreement

 
 

by 1911 that eating too much polished rice caused
beriberi (witness the resolution of the Far East Associa-
tion of Tropical Medicine), the reason for the ill effects
of polished rice and the good effects of the rice skin
was by no means settled. In addition to the toxin-
antidote theory held by Eijkman, Braddon, and others,
and the protective substance-deficiency theory held
by Grijns and Fraser and Stanton, there were other
reasonable suggestions: a deficiency of fat, a deficiency
of phosphorus, a deficiency of nitrogen, an excess of
carbohydrate, a lack of a particular phosphorus-contain-
ing substance called phytin (Williams 1961, pp. 14-15).

When Funk and the first of several collaborators,
E. A. Cooper, set to work analyzing extracts from rice
skins in 1911, they had very little idea what to look for.
The extant literature, they remarked, gave very few
clues to the chemical nature of the protective substance
from rice polishings, except that it seemed to be neither
a salt or a protein.

Cooper and Funk's first experiments sought to learn
whether the substance could still cure beriberi after it
was subjected to extensive chemical manipulations,
whether it had a simple or complicated chemical struc-
ture, and whether it belonged to a known class of chem-
ical compounds. They quickly showed that “it is very
improbable that polyneuritis is the result of a deficiency
in phosphorus compounds.” The active extract they
obtained also lacked carbohydrate or protein groups,
although it did include a significant amount of nitrogen.
And, as others had found, very small amounts of the
extract sufficed to cure beriberi in pigeons (Cooper
and Funk 1911, pp. 1266-67; Funk 1911, p. 400; Funk
1912a, p. 149).

Funk coined the word ‘“‘vitamine’’* for his 1911
paper in the Journal of Physiology to describe the
nitrogen-containing substance he and Cooper had
extracted from yeast and rice skin. But the staff at the
Lister Institute, to whom he was required to submit
drafts of his research papers, and the editors of the
Journal of Physiology disliked the new word. Their
opposition was quite sensible: the substance had not
been proved to be an amine or amino acid — as the
word implied — and, in general, the indiscriminate
coining of words in science led to confusion. Funk was
not obliged, however, to show drafts of review articles
to his colleagues at the Institute, and at the suggestion
of a fellow Polish scientist, he wrote an article on “The
Etiology of Deficiency Disease’’ for the widely read
Journal of State Medicine in 1912 (Harrow 1955, pp.

41-43). Here he was free to introduce and explain what
he meant by his catchword, ““vitamine.”’

It is now known that all of these diseases (beriberi,
polyneuritis, epidemic dropsy, scurvy, experi-
mental scurvy in animals, infantile scurvy, ship
beriberi, pellagra), with the exception of pellagra,
can be prevented and cured by the addition of
certain preventive substances; the deficient sub-
stances, which are of the nature of organic bases,
we will call “vitamines;’ and we will speak of a
beriberi or scurvy vitamine, which means a sub-
stance preventing the particular disease (Funk
1912a, p. 164).

Although Funk did not give the etymology of “vita-
mine’’ in this paper, it clearly was a compound of vita,
“life’” in Latin, and amine, a nitrogenous base. Thus,
a ‘'vitamine’’ meant a nitrogenous amine which is
necessary to life: a much larger claim than ‘‘a substance
preventing the particular disease,” and a claim that
made Funk's colleagues at the Institute and on the
Journal of Physiology uneasy. In later years Funk
protested that he did not mean that a// vitamines had
to be amines, but this point was not clear in his early
papers and caused considerable confusion (Funk 1922,
p.169,n. 1).

In his essay of 1912, Funk also surveyed the evidence
for grouping human and experimental beriberi, scurvy,
and ship beriberi under the general category of ‘“defi-
ciency diseases,’”” and perspicaciously argued that pella-
gra and possibly rickets also belonged to this class
although the vitamines involved were probably different
from those of beriberi and scurvy. He told of the at-
tempts by himself and other investigators to extract the
active substance, the beriberi vitamine, from rice skins,
yeast, and Katjang idjoe beans. Speculating on the
possible chemical and metabolic relationships between
the beriberi vitamine and the scurvy vitamine, it seemed
likely to him that the animal body could transform the
scurvy vitamine into the beriberi vitamine, but not
vice-versa. And, based on what he knew of the experi-
ments by Osborne and Mendel and by Hopkins with
simplified diets supplemented by milk, Funk supposed
‘that the substance facilitating growth found in milk
is similar, if not identical, with the vitamines described
by me’’ (Funk 1912a, p. 169).

The reactions to Funk's work were mixed. In general,
his attempts to isolate the active substance in rice skin
were greeted with enthusiasm. Only a few weeks after

 
Cooper and. Funk's preliminary 1911 communication
on rice-skin extracts in Lancet, a column in Lancet
described how a German explorer in New Guinea had
successfully prevented beriberi among the members
of his expedition by eating a pottage of red rice and
Katjang idjoe beans cooked together every day. The
anonymous Lancet writer remarked on the new progress
of knowledge about the disease:

In future we are to expect that, thanks to the
work of Mr. E. A. Cooper and Dr. Casimir Funk
(The Lancet, Nov. 4, p. 1266), the leader of an
expedition will be able to take all the special
substance required to keep beriberi away from his
men in a one-ounce bottle in his pocket. Of such
are the triumphs of medicine. (Anonymous 1911c)

But the proposal of the new word, vitamine, and its
theoretical implications aroused much controversy.
During the next ten years Funk campaigned vigorously
on behalf of his idea. In 1914 he published a long
German monograph, Die Vitamine, which was revised
and translated into English in 1922. Although he moved
several times — from England to Canada, from Canada
to the United States, then to Poland, to Paris, and back
to the United States in 1939 — Funk continued to do
research on vitamines and to publish papers on his work
in English, German, and Polish (Harrow 1955, pp. 55-
98). Less than five years after Funk coined the word,
"“vitamine’’ became a widely used and accepted term in
scientific and popular writing. In September 1915, for
example, Scientific American published a condensation
of an article on “"Vitamines and Their Importance for
the Maintenance of Health.” A year later an editorial in
Science, "A New Phase in the Science of Nutrition,”
described the progress of vitamine research and showed
how well Funk's term caught on:

The word “vitamine’’ has come into our vocabu-
lary since the latest dictionaries were published.
Etymologically it means an amine that is essential
to life, and it was coined by C. Funk as a generic
name for a group of substances, of unknown
chemical composition, small quantities of which
appear to be a necessary constituent of a whole-
some human diet. . .An absence or insufficiency
of vitamines in the diet brings on diseases now
known as ““avitaminoses’’ or ‘‘deficiency diseases,’’
of which scurvy and beriberi are the principal
representatives. Science already recognizes two
vitamines — viz., antiscorbutic vitamine, which

36

prevents scurvy, and antineuritic vitamine, which
prevents beriberi in man and polyneuritis in birds.
There may be others.

The investigation of the vitamines has made
great strides in the past two years. The subject
is beginning to crop up in the newspapers and in
general literature, not to mention the small talk
of the dinner table, where everything on the

menu invites classification from the point of
view of the ‘vitaminologist.”” (Science 1916,
p. 453)

By the early 1920's writers were using the term
metaphorically: “A book. . . .so full of the vitamines
of literature,” “The vitamines of the spirit and. . . .of
true religion’’ (Oxford English Dictionary Supplement,
1933). But, although widely used, the word and the
concepts it stood for still upset many scientists. As
late as 1948, the eminent physiologist and pharmacol-
ogist, Sir Henry Dale, regretted that Hopkins had not
used “the right, which would have been generally
accorded to him (in view of his contribution to vitamin
research)’’ to suppress so inappropriate a term (Dale
1948, p. 131). Osborne and Mendel, in their second
1913 paper, “The Influence of Butter-fat on Growth,”
wrote that butterfat probably did contain ‘‘something
analogous to the so-called vitamines which Funk con-
siders to be necessary for life,” but they saw some
important objections to Funk's generalization.

Without minimizing the importance of the new
field of research and the new viewpoints in nutri-
tion which are presented by these recent findings,
we may nevertheless hesitate to accept the ex-
treme generalizations which have already been
proposed on the basis of the evidence obtained
largely from the investigation of pathological
conditions. . . .It is still rather early to generalize
on the role of accessory “vitamines’’ when the
ideal conditions in respect to the familiar funda-
mental nutrients and inorganic salts adequate for
prolonged maintenance are not completely solved
(Osborne and Mendel 1913b, pp. 429-30).

They argued further that a substance which maintained
health, like Funk's beriberi and scurvy vitamines, might
be a very different kind of thing from their butterfat
accessory factor which promoted normal growth. In any
case, their butterfat growth-promoting substance was
not nitrogenous — the one chemical characteristic Funk
seemed to insist upon by his use of the suffix amine.

 

 
 

McCollum made similar criticisms in his popular

lectures on nutrition in 1918. He disliked the vita
prefix because it implied that vitamines were more
essential to life than, for example, the indispensable
amino acids. And, McCollum felt, Funk had exaggerated
the number of deficiency diseases, erred in his chemical
description of the curative substances, and foolishly
denied the significance of the fat-soluble substance.
The popularity of Funk's word, McCollum said bluntly,
was deplorable: “There has become fixed in the minds
of students of nutrition and of the reading public an
altogether extravagant idea regarding the importance
of the substances to which Funk gave the name ’vita-
mines’ ” (McCollum 1918, pp. 84, 113-14). Hopkins
and Abderhalden preferred other terms to express the
idea of indispensable dietary constituents of undeter-
mined chemical composition: ‘accessory food factors,”
“food hormones,” ‘‘nutramines’’ (Needham and Baldwin
1949, p. 166; Abderhalden 1919, p. 39).

Despite (or perhaps because of) these disagreements
about words and the things they stood for, more and
more scientists became interested in the nature of
vitamins and in the practical applications of what
McCollum in 1918 called ‘‘the newer knowledge of
nutrition.” Funk's former colleagues at the Lister
Institute (he had taken an appointment at the London
Cancer Hospital in 1913) made vitamin research their
main contribution to the war effort: they studied the
quantitative distribution of vitamins in different foods;
and, in response to an epidemic of beriberi among
Australian soldiers stationed on Lemnos, they prepared
vitamin-concentrates from yeast and eggs to supplement
army rations. Funk's assistant, Jack C. Drummond,
performed some early experiments on the effects of
vitamins on tumor growth rates and worked with Hop-
kins on the wartime Food Committee of the Royal
Society, making recommendations about food rationing
and vitamin enrichment of margarine. In the United
States, McCollum, with various collaborators, continued
his research on rat diets, trying to distinguish among
the various indispensable food complexes by their dif-
ferent physiological effects. R. R. Williams was given
unofficial permission by his biochemist-chief at the
Food and Drug Service to work part-time with Atherton
Seidell on the isolation and synthesis of the beriberi
vitamin, even though ‘‘at that time, of course, vitamins
were not recognized as having a legitimate place in
food chemistry” (McCollum 1918, passim; Williams
1961, p. 107).

37

 

In the Netherlands and Java, Eijkman and his co-
workers continued their studies of beriberi and the
active substance in rice skins; similar research was under-
way in Japan. Pellagra and rickets, which Funk and
Hopkins had guessed might be due to vitamin deficien-
cies, received new attention from physicians, scientists,
and public health services in American and Britain.

In 1920 Jack Drummond helped lessen the remaining
disagreement in the new field by proposing a reform of
nomenclature. He acknowledged the great convenience
of having a single word to name all of the ‘‘so-called
accessory food factors’’ and noted the confusion that
accompanied the proliferation of synonyms for Funk's
vitamines. But the word vitamine, despite its wide
adoption by 1920, was still unfortunate because ‘‘the
termination ‘-ine’ is one strictly employed in chemical
nomenclature to denote substances of a basic character,
whereas there is no evidence which supports his (Funk's)
idea that these indispensable dietary constituents are
amines’ (Drummond 1920, p. 660). Drummond sug-
gested that the final e in “‘vitamine’’ should be dropped.
The result, “vitamin,” would fit under the Chemical
Society's nomenclature rule, which allowed ‘a neutral
substance of undefined composition to bear a name
ending in ‘-in’."" The various individual vitamins could
then be called by the letters of the alphabet which had
already been used to differentiate among them: vitamin
A, vitamin B, vitamin C. Funk opposed the change
because, he said in 1922, “I still believe in the nitrog-
enous nature of these substances,’”” and he continued
to call them by the name he had invented until 1937
(Funk 1922, p. 39 n. 2; Harrow 1955, p. 200). Other-
wise, the new spelling was adopted rapidly, although, as
we shall see, the designations of individual vitamins
presented other difficulties. 2

If the “young science of vitamins'’ needed further
legitimation it was provided in 1929 by the award of
the Nobel Prize in Medicine and Physiology to Christian
Eijkman and Sir Frederick Gowland Hopkins for their
"discoveries of the antineuritic and the growth-promot-
ing vitamins. . . .which. . . .are foundation stones of the
science of vitamins’ (Liljestrand 1929, p. 198). Hopkins
used the occasion to recount the early history of vitamin
studies, paying tribute to the foreshadowings of Lunin,
Socin, and Pekelharing, noting Grijns’ correct interpreta-
tion of Eijkman’s experiments on chicken beriberi, and
assessing the work and writings of Casimir Funk.

The award to Hopkins must have made Funk bitterly
angry. Three years before, Funk had protested in a letter
 

to Science that Hopkins did not deserve to be called
“the discoverer of vitamines,’’ that Hopkins’ 1912
paper came ‘‘so late that it exerted a relatively small
influence on the development of the whole subject,”
and that Hopkins’ earlier work, described in the 1906
speech, had been unknown to other workers until
1912 (Funk 1926, pp. 455-56). Hopkins’ conclusion
in the Nobel Prize lecture that Funk had ‘not received
too much, but too little credit for his vitamin research
as a whole’ was hardly consoling, since Hopkins still
claimed priority for his own experiments and ideas on
the physiological functions of vitamins (Hopkins 1929).
As in all priority disputes, both sides had justification
for their rival claims to recognition. It is idle for us to
try to apportion credit or judge the relative significance
of their various contributions, not to mention those
of their predecessors like Pekelharing and Eijkman or
their contemporaries like McCollum and Osborne. But
we should underscore one point: the rapid acceptance
of the idea of vitamins was probably as much due to
Hopkins’ and Funk's enthusiastic, skillful evangelizing
as to the two biochemists’ actual scientific work on the
chemistry and physiology of accessory food factors
(Becker 1970, pp. 159-161). .

The Race for Vitamin B

No doubt scientists would have tried to isolate,
analyze, and synthesize the anti-beriberi factor in rice
skins and the growth-facilitating factor in butterfat
even if there had been no theory linking the two, for
it was clear that each of these substances was of physiol-
ogical and medical importance. But the vitamin hypoth-
esis made it all the more imperative to obtain the sub-
stances in pure form. Only then could one know wheth-
er the crude extracts contained more than one active
substance, whether vitamins did constitute a new class
of chemical compounds (as Funk seemed to assert),
and whether the various vitamins all performed similar
physiological functions. At least four different research
teams were engaged in the effort to isolate the beriberi
vitamin, a task of very great difficulty. Then, once the
pure vitamin had been isolated, it was possible to work
out its correct structure. Once the structure was known,
the synthesis of vitamin B; in turn was a comparatively
simple albeit also lengthy task.

R. R. Williams, who was deeply involved with every
stage of this endeavor, estimated in 1938 that no other
substance in the history of biochemistry had cost so
much to isolate and identify as vitamin By: “The first

38

gram of pure vitamin must have cost an aggregate of
several hundred thousand dollars’ (Williams and Spies
1938, p. 138). That cost is only one measure of the
importance, both theoretical and practical, that scien-
tists attached to gaining knowledge of the anti-beriberi
substance. The quest for vitamin B; served as a school
for biochemists from 1912 to 1940. ‘To mention all
the names of those who have participated in some
phase of the project,” Williams wrote, ‘is to call the
roll of half the mature biochemists in England and the
United States. The project bulked equally large upon the
horizon of Dutch, Japanese. . .French (and, somewhat
later, German) biochemistry. . .”" (Williams and Spies
1938, p. 138).

The high cost in labor, time, and materials was largely
due to the nature of the vitamin itself. To those who
worked on its isolation, the vitamins ability to act
effectively in very small doses raised two immediate
problems: the anti-beriberi factor was to be found in
nature only in very small quantities, and its presence
in crude extracts was hard to assay.’ The enormous
quantities of rice skin or yeast that it took to yield
even a tiny bit of the vitamin astonished everyone
who worked on the problem. For example, Jansen and
Donath, who carried on the long tradition of Dutch
beriberi research in Eijkman’s laboratory in Djarkarta,
began with 100 kilograms of rice bran to obtain 100
milligrams of pure vitamin (Jansen 1956, pp. 274-277).

The problems involved both in extracting a tiny
bit of vitamin from tons of rice bran or from yeast and
in measuring its ability to cure beriberi were complicated
by a confusion that was as much a dispute over theory
as it was a problem with chemical techniques. During
the first years of vitamin research, the leading research-
ers could not agree how many vitamins there were.
Funk, for instance, believed for several years that only
the beriberi vitamin and the scurvy vitamin fit his
criteria for a vitamin. Accordingly, he at first rejected
McCollum'’s fat-soluble growth factor because it did not
cure beriberi (or any other known deficiency disease)
and because it was not an amine (Funk 1922, p. 117;
Funk 1925, pp. 157-58). McCollum, in turn, insisted
that only his fat-soluble growth factor, ‘‘fat-soluble A”,
which did cure an eye disease, and Funk's anti-beriberi
factor, “water-soluble B”’, were true vitamins. His early
experiments led him to assert that scurvy, rickets, and
pellagra were not vitamin deficiency diseases (McCollum
1918, pp. 30 ff). But the nature of vitamin B — as
Drummond had renamed the beriberi vitamin and

 

 
 

“water-soluble B’ — was itself in question. McCollum
showed in 1918 that ‘‘water-soluble B" was as necessary
to the growth of rats as ‘‘fat-soluble A”. Was vitamin B
then a single substance with several distinct physiological
functions, or was vitamin B a mixture of different active
substances?

Early in the 1920's Eijkman and Jansen, among
others, declared their belief that the water-soluble
growth factor which could be extracted from yeast
was not identical to the beriberi-preventing factor
(Williams and Spies 1939, p. 130). Jansen and Donath
clearly made this a working assumption in their choice
of an assay for vitamin B — only the cure or prevention
of beriberi could serve as a valid test for the presence
of the beriberi vitamin. Their decision was vindicated in
1926 by Smith and Hendrick, who demonstrated that
the anti-beriberi factor in yeast could not survive pro-
longed heat, while the rat-growth factor in yeast did
retain its activity after heating (Williams and Spies
1938, pp. 130-31). Thus, vitamin B was not.a single
substance but rather a complex of at least two vitamins:
the thermolabile, anti-neuritic factor (that would be
called vitamin Bj, aneurin, or Thiamine), and the
thermostabile, growth-promoting factor (Dutcher 1928,
pp. 206-209).

Despite the many problems of technique and theory,
Jansen and Donath succeeded in isolating almost pure
crystals of the beriberi vitamin in 1926. Williams, who
also was working intensively to isolate the vitamin,
regarded this feat as a “’landmark. . . .example of a
systematically planned and executed pursuit of a chemi-
cal objective” (Williams and Spies 1938, p. 139). After
eight years of labor, the Dutch chemists obtained 100
milligrams (1/280 of an ounce) of the almost pure
substance. They sent ‘‘some scores of milligrams’’ to
Eijkman, who had the pleasure of confirming their
claim that this substance was the vitamin and that
astonishingly small amounts of it could cure or prevent
beriberi in birds (Jansen 1956, p. 274-77).

Jansen and Donath’s long and tedious work had
shown that the anti-beriberi vitamin could be isolated
from natural sources, and, they believed, they also
had determined its correct empirical formula. Other
groups immediately set out to repeat and modify
the isolation process, and to check Jansen and Donath’s
analysis of thiamine’s chemical components. In 1931,
a team of chemists at Gottingen led by A. Windaus
found that Jansen and Donath had made a critical error
in their analysis: they had overlooked the presence of

39

sulphur in the thiamine molecule. As Williams com-
mented, ‘What a shock it must have been to Jansen and
Donath to learn of this mistake after all the years of
grueling work they had expended on the isolation! ”
(Williams 1961, p. 117).

Two years later, in 1933, successful isolation was
also reported by R. A. Peters and his colleagues in
England, and by Williams’ group in the United States.
Williams’ group confirmed Windaus’ empirical formula,
and, by several innovations in the isolation process,
succeeded in improving the yield of pure crystalline
thiamine by four or five fold.

Now an intense race began to determine the structure
of thiamine and then to synthesize the vitamin (see
Williams 1961; Wuest 1962). The race was triggered
not only by the desire of chemists to understand how
thiamine was made and to synthesize it, gaining undeni-
able prestige in the process. The pharmaceutical industry
knew that the commercial rewards, too, would be high
for the company that acquired patent rights to manu-
facture the anti-beriberi vitamin. Thus, impelled by a
variety of motives, three major groups of researchers
and pharmaceutical companies pursued the structure
and synthesis of thiamine: R. R. Williams et al. in
the U. S., at first independently, but later supported
by Merck and Co.; A. R. Todd and F. Berjel in England,
sponsored by the Swiss company, Hoffman-La Roche,
Ltd; and, in Germany, H. Andersag and K. Westphal in
the Elderfeld Laboratories of the giant chemical firm,
I. G. Farben.

Scientific priority in the race fell to R. R. Williams
and his colleagues in the U. S., who first published the
complete synthesis procedure in August 1936. Not
having realized that his work on thiamine had significant
commercial interest, Williams was surprised to find
that he was engaged in a highly competitive race, and
even more surprised to find himself embroiled in a legal
dispute over patent rights with I. G. Farben. Williams
and his colleagues had assigned the patent to a nonpro-
fit Research Corporation, to insure that the profits
from the manufacture of vitamins would be used to
support scientific research and to eradicate dietary
diseases. The courts ultimately awarded the patent
rights in the United States and Canada — which soon
became the largest market for vitamin B in the world —
to Williams et al., Research Corporation, and its two
licensees, Merck and Co. and Hoffman-La Roche. After
eight years of effort, we recall, Jansen and Donath in
1926 had finally extracted 100 milligrams of crystalline

 

 
 

thiamine from natural sources. Could they, one wonders,
have envisaged that by 1950 the U. S. manufacturers
of synthetic thiamine would be producing 100 metric
tons a year!

Nomenclature continued to be a problem for several
more years after thiamine had been analyzed and synthe-
sized. Vitamin B; was a widely accepted term, but
seemed to belong too much to the era of confusion over
the heterogeneity of vitamin B. Jansen proposed ‘‘aneu-
rin” as an abbreviation for ‘‘anti-neuritic vitamin,’
a word still used in the British Pharmacopeia. But the
American Council of Chemistry and Pharmacy of the
American Medical Association rejected this name be-
cause it made a therapeutic claim for the substance,
and because it could be confused with ‘‘aneurism.’”
The Japanese vitamin researchers tended to use the name
“oryzanin,” while R. A. Peters in England preferred
“torulin” — words that referred to the source of the
vitamin in rice and yeast. In 1937 R. R. Williams sug-
gested that, since ‘aneurin’ had met with such objec-
tions in the United States, it might be convenient and
acceptable to use a name which reflected the vitamin's
chemical peculiarities: ‘‘thiamin,”” where the thia-
prefix referred to the sulphur atom and thiazole ring
(Williams and Spies 1938, pp. 134-35). Later, the
American Chemical Society noted the presence of an
amino group in the molecule and changed the name
to “thiamine” — a small indirect victory for Casimir
Funk's original nomenclature.

Thiamine, Coenzymes, and Carbohydrate Metabolism

While organic chemists were hard at work isolating,
analyzing, and synthesizing pure vitamin By, physiol-
ogists and biochemists were busy trying to understand
the vitamin’s role in metabolism. Unfortunately, the
organic chemists and the biochemists and physiologists
of the 1920s and 30s could not help each other with
their tasks, for the chemical structure of the vitamin
offered no clues to its functions, and vice versa. There
was no chemical test for the presence of vitamin By, for
instance, that would determine its, distribution in the
tissues, and the low yields of the early isolation proce-
dures forestalled any systematic physiological experi-
mentation with the pure crystals. As a result, the concur-
rent investigations of the chemistry and physiology of
vitamin B; did not converge until 1937, when the newly
synthesized vitamin was used to confirm the identity
of thiamine with cocarboxylase, a coenzyme which had
just been shown to play a major role in carbohydrate
metabolism.

40

 

Almost as soon as an accessory food factor was
postulated as the cause of beriberi, scientists began
suggesting a variety of ways that such a factor might
act in metabolism. Eijkman’s original hypothesis was
that it neutralized toxins produced by starches. The
edema suffered by many beriberi patients made some
observers think that the vitamin was involved in water
metabolism, while others felt that the vitamin was
involved in the body's ability to use phosphorus. Funk's
discovery that the vitamin contained a pyrimidine ring
suggested to him that the vitamin might have some-
thing to do with nucleic acids, although the functions
of the latter were completely obscure at the time. The
rapidly accumulating knowledge of hormones and
their importance in metabolism made other early re-
searchers, such as Hopkins, Schaumann, and Funk think
that vitamins might work as ‘’exogenous hormones,”
that is, hormones that had to be supplied by nutriments
rather than by biosynthesis within the body. Somewhat
akin to this idea was Hopkins’ early view of “nutritive
errors’’: the effects of the missing food factors were
comparable to the ‘inborn errors of metabolism’’
described by his close friend, Sir Archibald Garrod
(see Chapter 5). Thus, the accessory food factors might
be necessary at particular stages of metabolic pathways,
although Hopkins could not specify whether the factors
served as catalysts or substrates (Hopkins 1906, p. 396).
In 1911 Funk suggested that vitamins might serve as
“mother-substances,”” precursors to other essential
metabolites (Funk 1914, p. 6). Because such small
amounts of vitamins had such striking effects, Seidell
among others speculated that they might be related to
enzymes (Seidell 1924, p. 440).

Funk and others considered yet another possibility,
which proved to be the best guess about the function of
the beriberi vitamin. In 1914 Funk observed that if
pigeons on a vitamin-free diet were fed extra carbohy-
drates, they developed polyneuritis more rapidly.
Experiments on pigeons fed with various combinations
of carbohydrates and vitamin extracts suggested that
vitamin-free artificial diets with a high proportion of
carbohydrates cause a ‘marked disturbance of the
carbohydrate metabolism’ which could be quickly
reversed by the vitamin. Braddon and Cooper came to
similar conclusions at the same time (Funk and Schén-
born 1914, pp. 328-331).

Although the idea that vitamin B; was somehow
involved in carbohydrate metabolism gave a focus
to research, it was not as helpful as the vitamin research-
ers must have hoped, for carbohydrate metabolism was

 

 
in itself one of the central problems of biochemistry.
A common refrain in historical accounts of develop-
ments in biochemistry is, “the process was turning
out to be much more complex than had been imagined
ten years before’ (Fruton 1972, p. 343; Peters 1939,
p. 1071, note). In the case of carbohydrate metabolism
and thiamine, it took several decades before the varied
experimental observations of fermentation, glycolysis,
respiration, and vitamin activity could be sorted into a
coherent scheme for the breakdown of sugar and the
tapping of its energy.

Two quite different lines of biochemical work led to
the conclusion in 1936-37 that vitamin B; acted as a
coenzyme in the reactions of pyruvic acid, an important
intermediate in both the anaerobic fermentation of sugar
to alcohol and carbon dioxide, and the aerobic brf§ak-
down of sugar in respiration to carbon dioxide and
water. The research by Karl Lohmann, which culminated
in the isolation of cocarboxylase and the recognition of
this coenzyme as the phosphoric ester of thiamine, was
part of a long, intensive investigation into what is now
called the Embden-Meyerhof pathway: the anaerobic
degradation of glucose to pyruvic acid, and thence
to ethanol and carbon dioxide in yeast (fermentation),
or to lactic acid in muscle (glycolysis). The second line
of research, that by R. A. Peters and his collaborators,
was specifically aimed at understanding the cell’s need
for thiamine: they wanted to pinpoint the lesion caused
by the vitamin deficiency, but they also realized that
their work ought to cast some light on the details of
carbohydrate metabolism.

Karl Lohmann worked as a senior staff member in
Otto Meyerhof’s research laboratory from the mid-1920s
to 1936, where his ability as a superb organic chemist
beautifully complemented Meyerhof’s keen scientific
imagination in their studies of glycolysis, muscle con-
traction, and fermentation (Proc. Conf. Hist. Devel.
Bioenerg. 1973, pp. 70-73, 169). Among his many
accomplishments, the achievement for which Lohmann
is best known was his isolation of adenine triphosphate
(ATP) in 1929. Later, ATP was shown to be the com-
pound which trapped the free energy to drive other
reactions in the cell. Although Lohmann recognized
some of the implications for energy transport by ATP,
he was chiefly interested in the compound as a coen-
zyme required for the transfer of phosphate to and
from intermediates in the pathway of glycolysis and
fermentation (Cori 1973, pp. 163, 166; Fruton 1972,
pp. 366-69).

41

The question Lohmann wanted to answer once he
had isolated ATP was: what does the coenzyme ATP
have to do with the coferment of zymase discovered by
Harden and Young in 1906?” It was through the pursuit
of this question, in a series of complex biochemical
studies, that Lohmann and Schuster in 1937 announced
the purification of a new coenzyme, cocarboxylase, and
proved that ‘‘the organic ‘ground substance’ of cocar-
boxylase, is diphosphorylated aneurin (vitamin By”
that is, ‘‘cocarboxylase is diphosphorylated aneurin
(vitamin By)" (Lohmann and Schuster 1937, p. 300).

Unfortunately, it is not clear from Lohmann’s ac-
count of his investigations when or how he first sus-
pected the identity of the coenzyme as thiamine diphos-
phate. The publicity that had been given to R. R.
Williams’ recent analysis of thiamine's structure, and the
subsequent race to synthesize the vitamin may well have
alerted Lohmann to compare the two compounds.
Obviously, only the availability of pure crystals of
thiamine from natural sources and from Williams’
synthesis made a definitive identification possible.

There was another reason, though, for Lohmann to
think of his coenzyme in terms of vitamins. Between
1932 and 1935 Warburg, Kuhn, and Theorell had
shown that riboflavin (vitamin B, in one nomenclature)
was the coenzyme for the so-called “yellow enzyme’’
which, according to Warburg, shuttled hydrogen from
the oxidation of sugar to the respiratory chain to react
with oxygen (Ball 1973, pp. 98-99). Lohmann men-
tioned the work on riboflavin in the discussion part of
his cocarboxylase paper and drew attention to another
similarity between the two vitamins: not only were
they both the ‘ground-substances’” of coenzymes,
but they also needed phosphate groups to be added onto
the vitamin molecule before they could act as coen-
zymes. It was a point that the discoverer of ATP was
bound to notice. It is also proof that Lohmann did
not yet know that the nicotinic acid amide in Warburg's
other coenzyme, DPN, was the anti-pellagra vitamin,
although Warburg himself had suggested this identity.
When he first crystallized nicotinic acid amide crystals
from DPN in 1934, Warburg declared, “| am quite sure
this will turn out to be a vitamin.” But despite his
research on the coenzyme function of riboflavin, War-
burg was not interested enough in vitamins to follow
up his hunch about nicotinic acid amide (Theorell 1962,
p. 2). Thus, it was not until late 1937, after Lohmann
and Schuster’s paper on cocarboxylase, that Conrad
Elvehjem published his identification of niacin as yet
another vitamin which acts as a phosphorylated struc-
ture in a coenzyme. Not surprisingly, the identification
within so short a span of time of three members of the
vitamin B complex as parts of coenzymes involved in
major metabolic pathways suggested that all vitamins
have coenzyme functions, setting in motion a great deal
of new biochemical research.

The second major line of research leading to the
identification of vitamin B;’s coenzyme function was
that pursued by R. A. Peters and his colleagues at
Oxford. While Peters and Lohmann arrived, indepen-
dently, at the same conclusions about thiamine's role in
intermediary metabolism, their work was strikingly
different in both techniques and goals. Karl Lohmann,
as we have noted, was an organic chemist, whose work
relating to vitamin B; was part of a complex series of
basic biochemical analysis being conducted by Meyer-
hof’s laboratory group. R. A. Peters, on the other hand,
had been trained as a physician, and for personal and
professional reasons ‘‘could never forget the hospital
and the wish to improve care for people’’ (Peters, per-
sonal communication). Peters saw his research on thia-
mine as an attempt to explain the pathology of vitamin
deficiency in biochemical rather than histological or
anatomical terms. He introduced the striking phrase
“biochemical lesion,”” to ‘crystallize the idea that
pathological disturbances in tissues were initiated by
changes in their biochemistry’ (Peters 1963, p. 1).
Although the ultimate aim of Peters’ research was to
pinpoint a derangement in a biochemical pathway,
his use of pigeons as an assay forced him to keep in
mind the gross consequences of the biochemical lesion
upon the whole organism.

After completing his clinical studies, Peters served
as a medical officer in France until he was recalled to
England at the request of the eminent physiologist,
Sir Joseph Bancroft, ‘to work on antidotes to gas
poisoning’’ (Peters, personal communication). It was
in this particular context of war-impelled research that
Peters’ attention was first directed to vitamin Bj.
In 1920, working in Hopkins’ laboratory at Cambridge
on the effects of poisons on protozoa, Peters found that
his protozoa would not grow on their artificial medium
unless an alcoholic extract of yeast was added, and thus
his interest was directed to vitamin B. Beginning in
1922, and continuing after his appointment as professor
of biochemistry at Oxford in 1923, Peters began the
effort to isolate vitamin B; from bakers’ yeast.

42

“When Jansen and Donath published their fascinating
isolation from rice polishings,’” Peters recalls, *‘l decided
to continue our work with yeast, because it would be-
come necessary ultimately to be sure that the vitamin
B; in yeast was the same compound as that in rice
polishings. And, we realized early that the Jansen and
Donath crystals were not quite pure’’ (Peters, personal
communication). Thus, along with the Windaus group
in Germany and Williams and Seidell in the United
States, Peters’ group pursued and eventually accom-
plished the goal of obtaining pure vitamin B; extract
from yeast.

From 1922/23 on, Peters states, his work on vitamin
B; “‘was part of a larger plan,” one inspired both by his
clinical training and his work as a biochemist. “’l thought
that by isolating one factor dealing with a specific
clinical condition, | could begin to clear up the muddle
as to how many B factors existed’ (Peters, personal
communication). Within this framework, the problem
of testing the vitamin activity of the yeast extract frac-
tionations led Peters to the question: how did the
vitamin deficiency produce the dramatic symptoms of
beriberi? He and his colleagues felt that the cure of
polyneuritic symptoms in pigeons was a more certain
sign of vitamin activity than either the prevention of
symptoms or the progress of normal growth. But, as
Williams and others had objected, it was all too easy
to produce false cures or remissions by injecting the sick
birds with glucose and water. So, during the mid-1920s,
Peters sought a reliable test of a cure. Opisthotonus,
the convulsive neck spasm which pulls the head of a
pigeon sharply back, seemed to be the most obvious and
important clinical sign of a genuine vitamin deficiency.
“Hence,” Peters recalls, “I sat down to make the pigeon
opisthotonus test quantitative and reliable. This | suc-
ceeded in doing by standardizing conditions of feeding,
and by never using birds which took over a month to
develop the head retraction, when other deficiencies
seemed to intervene’’ (Peters, personal communication).
If the opisthotonus appeared after a pigeon had lived
for a couple of weeks on a polised rice diet, Peters
found, it could often be relieved for a day or two by
glucose and water. But, if the neck spasm re-appeared
within a month or less on the deficient diet and could
no longer be relieved by glucose, then the only cure
was the vitamin (Peters 1963, pp. 6-8).

Study of the head retraction symptom, and their
observations of pseudo-cures with glucose, led Peters

 
to the next stage of research:

the convulsive state induced by the deficiency
drew my attention to the central nervous system
and provided the stimulus to examine this for
possibly enzymic changes; until then attention
had been focused upon the peripheral nervous
system, which had become emphasized wrongly
through the extensive use of the word “‘Poly-
neuritic.” (Peters 1963, pp. 8-9).

The temporary ‘‘cures’” produced by glucose suggested
that the glucose might counteract a low blood sugar
level in the sick birds. Comparison of the blood sugar
level in sick and normal pigeons did not give any real
answer, so Peters tried to lower the blood sugar in
healthy birds by insulin injections. As others had also
discovered, Peters reported in 1929, he found

that ordinary doses of insulin had no effect upon
the birds. Large doses generally gave convulsions
... .to my surprise the convulsions exactly resem-
bled those of avitaminosis. . . .So far as | know
this has not been previously pointed out. In view
of this fact, Mr. Kinnersley and | were led to
examine systematically the various features of
the carbohydrate “cycle” in the brains of avita-
minous birds. (Peters 1929, p. 272).

By 1936, the study of the ‘carbohydrate cycle”
undertaken by Peters and his associates had yielded
important findings about the function of thiamine. He
and his co-workers had shown as well that biochemistry
made a ‘new approach to pathological analysis’ possi-
ble. Working with rather large amounts of wet tissue
rather than with the cell-thick sections used by histolo-
gists, they could detect ‘‘changes too subtle to be
revealed upon the histological specimen, changes in the
behavior of essential enzyme systems present.” They
had, by this approach, first located the site of the
biochemical lesion of vitamin B; deficiency in the
lower parts of the brain, and then pinpointed the lesion
in the oxidation system of the 3-carbon stage (lactic
and pyruvic acid) of sugar metabolism. While Embden
and Meyerhof’s experiment had left open the possibility
that the presence of pyruvic acid was an artifact of
their techniques, Peters’ techniques proved that pyruvic
acid actually was a normal intermediary in carbohydrate
metabolism. They also had shown that the acute symp-
tom of the neck spasm in thiamine-deficient pigeons
was probably not due to a toxic build-up of pyruvic

43

acid, but to the deficiency of the energy which the oxi-
dation of pyruvic acid would normally produce. In
short, Peters and his colleagues had shown ‘‘that an
in-vitro research. . .which takes advantage of the
in-vitro labours of biochemists can be applied to in-vivo
events’’ (Peters 1936). Even in its unfinished state,
Peters’ work was a convincing demonstration of the
power of biochemical research to explain normal and
pathological phenomena at a new level of detail.

Lohmann’s isolation of cocarboxylase in 1937 was
a triumphant confirmation of Peters’ conclusions that
vitamin B; was the coenzyme directly concerned with
the metabolism of pyruvic acid. But Lohmann’s results
raised new questions. The first and easiest to answer
was: was there any important difference in the activity
of the free vitamin B; which Peters had used and the
phosphorylated vitamin B; which Lohmann had found?
Between 1937 and 1939 Peters’ group included the
Spanish biochemist, Severo Ochoa, who had just come
from Meyerhof’s laboratory at Heidelberg and thus knew
about Lohmann’s work first hand (Proc. Conf. Hist.
Devel. Bioenerg., 1973 pp. 169-170, 184). Ochoa
showed that both in brain and yeast, the free vitamin
had to be phosphorylated to become cocarboxylase
before it could act on pyruvic acid; the in vitro brain
tissue preparations Peters had been using luckily con-
tained the enzymes and phosphates necessary for this
step (Peters 1963, pp. 18-19).

A much more puzzling problem remained: what was
the aerobic oxidative reaction of pyruvic acid and
cocarboxylase in carbohydrate metabolism in the
brain? Lohmann had shown how pyruvic acid was
broken down to acetaldehyde by a simple removal of
carbon dioxide (i. e. decarboxylation) in the anaerobic
fermentation reaction of yeast. But Peters was dealing
with a system which included oxygen and in which
pyruvic acid was somehow completely broken down
by both oxidation (i.e. dehydrogenation) and decar-
boxylation to yield carbon dioxide, water, and energy.
The most satisfactory path for the oxidation of pyruvic
acid would have been the citric acid cycle which Hans
Krebs and W. A. Johnson proposed in 1937. Unfortu-
nately, when Banga, Ochoa, and Peters tried to test this
pathway, they found that only a few of the intermedi-
ates in the citric acid cycle would help speed the oxida-
tion of pyruvic acid (in the presence of cocarboxylase).
So in 1939 Peter's group was forced to conclude that,
in the brain at least, cocarboxylase set pyruvic acid
on some other important pathway which also required
the uptake of oxygen. They suggested that the pathway
might be the one outlined by Szent-Gyorgyi in 1937:
some of the compounds found in the Krebs cycle served
to transport hydrogen from pyruvic acid to the respira-
tory chain and ultimately to oxygen (Fruton 1972,
pp. 380-381; Banga, Ochoa, and Peters 1939a, b). With
this proposal, they claimed that ‘we may. . . .consider
that we know now the main facts about the biochemis-
try of vitamin B;"" (Banga, Ochoa, and Peters 1939a,
p. 1109).

Epilogue

Time would prove that Banga, Ochoa, and Peters
were in fact premature with their claim to know the
“main facts of the biochemistry of vitamin By.” Over
the next decade, Fritz Lipmann — with important
contributions from Ochoa and Feodor Lynen — clari-
fied the role of pyruvic acid as the ‘‘crossroads’’ or
“hub” of carbohydrate metabolism. In working out
the steps which link pyruvic acid to Kreb’s citric acid
cycle, Lipmann showed that cocarboxylase did indeed
mediate both the simple decarboxylation of pyruvic
acid in alcoholic fermentation and the oxidative de-
carboxylation of pyruvic acid in the first step of the
aerobic pathway (Lipmann 1971, pp. 27-54, 119-127).

Lipmann’s work marked the end of an era of vitamin
B; research. For those who had participated in the
discovery of vitamin-deficiency diseases, the identifica-
tion of vitamins, their chemical isolation and synthesis,
and finally the elucidation of their function in inter-
mediary metabolism, the pioneering excitement was
over and it was time to turn to other fields. But there
were still many questions about vitamin B; which
needed answers, many practical implications to work
out, and many new avenues of research that would be
opened up.

One major line of research, the practical application
of knowledge about the vitamins chemistry and func-
tion has, in effect, continued the original thrust of
Eijkman’s beriberi research. His original hope in studying
beriberi was to find the cause of the disease and then
to find a cure, but, as we have seen, Eijkman was more
successful at finding a cure for beriberi than at finding
out the primary cause.® It is impressive to see how, ever
since Eijkman, many of the scientists who worked hard-
est at basic research arising out of his observations of
beriberi’s cure also became leaders in the application
of their results to medicine and human nutrition. After
isolating vitamin B;, for example, Jansen immediately

used the process to prepare vitamin pills for beriberi
patients in the Dutch East Indies. R. R. Williams, in
turn, assigned the profits from his patent of thiamine
synthesis to the nonprofit Research Corporation, the
American Friends Service Committee, and Williams-
Waterman Fund for the Combat of Dietary Diseases,
in order to sponsor research in human nutrition and
dietary diseases (Williams 1961, pp. 168-189; Williams
1956). And, during World War Il, R. A. Peters turned
his knowledge of the pyruvate oxidase system back to
the problem of poison gases, which had indirectly led
him to the study of thiamine. He and his laboratory
were able to show how the arsenical gas, lewisite, inter-
fered with pyruvic acid metabolism, and they subse-
quently developed an effective antidote.

Medical researchers and physiologists also have
investigated a variety of factors which affect the thia-
mine requirements of micro-organisms, experimental
animals, and man: the proportions of fat, protein, and
total calories in the diet, the use of antibiotics or sulfa
drugs, the intestinal bacterial synthesis of thiamine or
its inhibitors, and interactions with hormones, minerals,
and other vitamins. Such work has suggested other
metabolic pathways in which thiamine could be in-
volved, and it has become clear that thiamine in its
phosphorylated form takes part in at least two dozen
biochemical reactions — more than any other coenzyme
known (Bhuvaneswaran and Screenivasan 1962, pp. 580-
585; Williams 1961, pp. 140 ff; Brin 1962; Breslow
1962; Gunsalus 1956).

From the vantage point of historical retrospect, we
can see that the scientific research inspired by the
study of beriberi was doné at two different levels of
complexity and detail, which correspond roughly to
the concerns of the science of nutrition and of the
science of biochemistry. For both sciences, the beriberi
and vitamin Bj; research posed important problems
and contributed to the theoretical foundations of the
field. When Eijkman began his investigation of the
relationship between diet and beriberi, nutritional
science was at a standstill. The results of the beriberi
research, coupled with the work on simplified diets,
gave the study of nutrition an entirely new entity to
deal with. What were these mysterious ‘vitamines’?
How many were there? How did their absence cause
disease? What was their chemical nature? The glory
and intellectual satisfaction that shortly before had
gone to the discoverer of a new microbial pathogen now
went to the scientist who discerned the deficiency of a
vitamin in a disease or who isolated or synthesized a
vitamin. The attempt to understand the function of
vitamins at a deeper level paralleled the development
of biochemistry as a discipline, and a remarkable number
of eminent biochemists cut their scientific teeth on the
problem of vitamin B;. The successful elucidation of
thiamine’s precise role in carbohydrate metabolism was
seen as a triumphant vindication of the primary program
of biochemical research, the dissection of intermediary
metabolism.

At the first level, it is easy to see how closely basic
nutritional research was tied to the clinical study of
disease. This connection is somewhat less direct, less
obvious in the biochemical stage of thiamine research,
yet even here the disease of beriberi continued to serve
as the inspiration for much of the work. It is probably
true that Lohmann’s work on cocarboxylase was aimed
at understanding one more piece of a complex metabolic
process, and as far as we know, he and Meyerhof had
no special medical question in mind. For them, the basic
research puzzle of carbohydrate metabolism was quite
difficult and interesting enough in itself. But for R. R.
Williams (and probably B. C. P. Jansen) the motives for
studying vitamin B, were certainly mixed. Williams has
testified how strongly his first-hand experience of the
ravages of beriberi in the Phillipines and the dramatic
cures with Vedder's rice-polish moved him to pursue
the problem to the end, despite the many ‘obstacles he
faced. Part of the urgency he felt in the race to synthe-
size thiamine arose from his certainty that his competi-
tors, all organic chemists in pharmaceutical firms, would
claim exclusive rights over thiamine manufacture for
their own firms and thus raise the price of thiamine
beyond anything that beriberi victims in Asia could
afford. And, Williams also found thiamine an absorbing
problem in organic chemistry.

When | began my work with Vedder in Manila,
and for twenty years thereafter, | never thought
of the antineuritic vitamin as something having
monetary value. It was merely a baffling scientific
problem, the solution of which would interest
the rice eaters of Asia. For several years | did not
visualize any probability that the knowledge of
its structure would be highly pertinent to the basic
science of nutrition, nor that its availability in
pure form would become a significant factor in
the economy or welfare of any people in the
West. | worked at the job of isolating it, part-
ly to justify my curiosity as to why or how it

45

worked, and partly as a humanitarian contribution
to the very poor and ignorant of Asia. (Williams
1961, p. 164)

For R. A. Peters, the motives are still harder to untan-
gle. In addition to his clinical interests, he gladly acknowl!-
edged the great influence that Hopkins and Hopkins’ out-
look had on his choice of problems and methods. His suc-
cess in finding the biochemical lesion of vitamin B; defi-
ciency proved, Peters has often said, how right Hopkins
had been to urge the unraveling of metabolic pathways
as the chief problem of ‘the dynamic side of biochemis-
try”’ (Peters 1963, p. 15; Peters 1929, p. 216; Peters
1957, pp. 371 ff). But Peters’ initial decision to study
vitamin B; was as a side issue which needed to be settled
before the research on the pharmacological effects of
poison gases could proceed. Then, we have seen, he
became absorbed by the challenge of isolating vitamin
B, as part of the larger puzzle of how many vitamin B
factors there were. Through this research, in turn, Peters
was led to search for the primary ‘lesion’ of thiamine
deficiency, a biochemical quest in part founded on the
bizarre character of the neck spasm in vitamin-deficient
pigeons and the astonishing speed of the cure. These
two phenomena caught his imagination in a way that
the tediously slow rat-growth test simply could not
match:

| always felt that at least for myself a very impor-
tant aspect of vitamin B studies was the dramatic
change in the polyneuritic pigeon, so-called, on
dosing with thiamine, i.e., the change from convul-
sive opisthotonus to normality. The impact which
these facts made upon myself was no more re-
markable than that upon students. . . .it was easy
to realize that something fundamental would be
found out if these events could be understood
and this is what induced me to study much further
this and the biochemical conditions of the brain.
(Peters 1963, pp. 8, 13; 1957, p. 373)

Although the biochemical puzzle quickly became the
major focus of Peters’ research, his use of the poly-
neuritic pigeons kept him from ever losing sight of the
in vivo effects of the biochemical phenomena he saw
in vitro. And it was this clearcut connection between
in vitro and in vivo events that made Peters’ explanation
of thiamine’s role in pyruvic acid oxidation in the brain
so convincing to both physicians and biochemists.

In the course of half a century, research on beriberi
and thiamine has directly contributed to two major
 

discoveries in basic science: the discovery of the exist-
ence of vitamins, and then the discovery of the role of
vitamins as coenzymes which catalyze crucial steps in
intermediary metabolism. Is there any prospect that
the study of beriberi can still lead to new fundamental
ideas in biology? Or has the study of vitamins at all
levels been so successful that, as some vitamin research-
ers have mournfully argued in recent years, there is
nothing left to do, that the field is complete and there-
fore dead? (Wuest 1962, p. 400; Schneider 1963,
p. 157; Zbinden 1962, p. 550.

History has often showed that it is unwise to speak
eulogies over a dead science, for too often the corpse
has proved to be a phoenix. At least two major questions
about beriberi and vitamin B; were not answered during
the golden age of vitamin research. How exactly do all
the terrible symptoms of beriberi — the burning of
the nerves, paralysis, edema, emaciation, heart failure,
convulsive spasms — follow from the initial biochemical
lesion, whether that lesion be the cocarboxylase defi-
ciency in pyruvic acid metabolism or the lack of thia-
mine in yet another process? And why is there such
variation among individuals and among species in their
susceptibility to thiamine deficiency? The first question
hints at the possibilities of new levels of complexity in
neurophysiology. The second suggests a new approach
to the interaction of environment and heredity (Schnei-
der 1963, pp. 162-169. It may still be premature to
claim that we know the main facts about beriberi and
vitamin B.
Notes Chapter 3

1.  “Thiamin’’ was later changed to ‘Thiamine’’ by the
American Chemical Society to reflect the presence of an amino
group in the molecule.

2. Between 1882 and 1906 Takaki succeeded in virtually
eliminating beriberi from the Japanese navy by adding European
foods to the Japanese rice-based diet; his theory was that the
ratio of nitrogen to carbon (i.e., protein to carbohydrate) in
the Japanese sailors’ diet was too small. A Dutchman, Van
Leent, had developed a similar theory in 1879 after observing
the differences in diet and the rate of beriberi between the
Europeans and the East Indians in the Dutch East Indian navy.
Eijkman, who knew Van Leent’s work, but not Takaki’s, was
able to show in 1896 that the amount of nitrogen in the rice
skin and germ was negligible, and that replacing such a small
amount of protein with protein from other foods would not
cure beriberi. Therefore, he concluded, beriberi was not caused
by a dietary deficiency of protein. He also initiated research
into the possibility that the rice skin might contain necessary
mineral salts. (Eijkman 1929, pp. 200-201).

3. Because Hopkins did not publish, it is hard to trace the
lines of his research except through his recollections and those
of his friends. He apparently began by performing experiments
like those of Lunin and Socin (although he was ignorant of
their work and Pekelharing’s) to convince himself that the
diet of purified basic constituents really was inadequate for
survival, let alone growth. He noticed that the mice grew fairly
well when fed some batches of commercial casein, while on
others they died quickly. The mysterious growth factor could
be extracted by alcohol from the growth-supporting casein,
leaving that casein incapable of helping the mice grow. Later,
Hopkins discovered that the yeast extract he had been using
to make the purified diets more tasty also contained this factor
and indeed was more effective than the casein extracts. (It was
at this point that he made his comments to the public analysts
in 1906.) Most of his research up to 1912 dealt with yeast
extracts and fractionations — time-consuming work because
each test had to follow the growth of rats over 4 to 9 weeks
(Dale 1948, p. 131; Hopkins 1912, pp. 454-460).

4. '"Vitamine'’ was the accepted spelling until 1920. Because
Funk's spelling had definite chemical and theoretical implica-
tions, we will use this spelling in discussing this early phase of
vitamin research.

5. The work that went into the development of reliable,
sensitive biological or chemical tests of thiamine's presence
could be the subject of a separate chapter, one that would
illustrate well the importance of technique in both clinical
and basic research. Significant assays developed for thiamine
after the time period covered in this chapter include that dis-
covered in 1936-37 by Bergel and Todd: an oxidation reaction
of thiamine to thiochrome, a compound which emits a strong
blue fluorescence that can be easily and accurately measured.
Then, in 1938, M. Lwoff devised a sensitive microbiological
assay for thiamine which used protozoa to test for the release
of thiamine by stimulated nerves (Sebrell and Harris 1972,
p. 147). These and other assays have been widely used to find
out how much thiamine is needed for the normal growth of
microorganisms, plants, animals, and people.

6. Over the next few years, the heat-stable factor was itself
shown to be a mixture of several physiologically and chemically
distinct substances. Ironically, Funk and a team of researchers
had identified one of these substances, nicotinic acid (niacin)
as early as 1911-12 in their attempts to isolate the beriberi
vitamin (McCollum 1957, pp. 310-311). But it was not until
1937 that niacin was proven to be the vitamin lacking in the
diets of pellagra victims, a deficiency disease fully as devastating
as beriberi (Etheridge 1972, p. 205 ff). While the intricate details
of the unraveling of the vitamin B complex do not concern us
here, it is important to realize how perplexing the multiple
properties of vitamin B were to the people who had to use
these properties as their only means of determining the presence
of the vitamin they hoped to isolate.

7. The discovery of coenzymes began in 1906, when Arthur
Harden and William John Young at the Lister Institute showed
that zymase from yeast could not ferment glucose unless two
other factors were present: phosphate and ‘‘a dialysable sub-
stance which is not destroyed by heat’ (Harden and Young
1906, p. 25; Fruton 1972, pp. 297, 344). In 1918 this second
factor — called coferment by Harden and Young, and cozymase
by Euler and Myrback in the 1920's — was found in animal
tissues by Otto Meyerhof. Then, in 1921, he and Gustav Embden
showed that coferment was as necessary to glycolysis in muscle
tissue as it was to alcoholic fermentation in yeast. Meyerhof,
Embden, and several other biochemists saw that this common
requirement for coferment implied a fundamental similarity
between the pathways of alcoholic fermentation and glycolysis
and, even more important, it implied a ‘unity of biochemistry’
among all kinds of living organisms (Fruton 1972, p. 346).
However, little was done to determine the chemical identity of
this necessary companion to zymase until the 1930's.

8. Beriberi is still the most important manifestation of vita-
min B; deficiency, and although much research has been done
on its pathology, cure, and prevention, it has remained a signifi-
cant public health problem in southeast Asia. Its modern victims,
though, are now more likely to be rural women and babies than
the soldiers, sailors, prisoners, and hospital patients who suffered
so often from beriberi at the turn of the century. In the course
of this century, more and more people have taken to eating
factory-polished white rice rather than milling their own rice:
the polished tastes and cooks better, it keeps better, and it
has a certain ‘social prestige.” To enrich the rich adds to its cost:
laws requiring enrichment are often hard to enforce; and so
beriberi persists (Salcedo 1962, p. 573; Sebrell 1962, pp. 566-
567). In the U.S. beriberi has never been a great problem, save
in conjunction with other dietary deficiencies like pellagra (now
rare, thanks to the general enrichment of staple cereal products)
or the general malnutrition of acute alcoholism.

 
Chapter 3
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51

 
CHAPTER 4
DISEASE AND THE DUCTLESS GLANDS

“By their diseases ye shall know them — the endo-
crines.” The title of this essay by J. H. Means aptly
characterizes the development of endocrinology, a field
to which his own clinically-oriented researches on
the thyroid contributed so greatly (Means 1960). For,
endocrinology is a science which grew out of the interest
of physicians in the malfunctioning of glands whose
functions were not yet well understood, and it has
continued to draw many of its problems from the
study of endocrine disorders.

In the pages that follow, we will look at the ways in
which research on endocrine disorders gradually revealed
the nature and functions of the hormones — the chemi-
cal messengers produced by the endocrine glands — and
the complexity and integration of the endocrine sys-
tem’s interactions. Our account of endocrinology’s
development defines four phases of research which,
though often overlapping in time and effort, are each
marked by the appreciation of a new level of complexity
in the functions of the endocrine glands. Phases one
and two, in which physicians and physiologists recog-
nized the effects of individual endocrine glands on
other parts of the body, and then discovered how glands
communicate with one another, will receive the most
detailed treatment in this chapter. For it was in these
phases of inquiry that problems of medicine raised a
fundamental biological problem, that of the nature of
the chemical regulation of physiological processes:
a problem around which endocrinology emerged as a
new field of research in the early years of the twentieth
century. To provide some understanding of the problems
that endocrinologists subsequently pursued we will
sketch, more briefly, the content of endocrinology’s
third and fourth phases. Phase three was marked by
discoveries about how the endocrine glands and the
nervous system influence each other's activities, while
in the fourth and current phase, endocrinologists and
molecular biologists seek to understand the elaborate
mechanisms of communication between the endocrine
system and the organelles of individual target cells.

The broad approach to the development of endocri-
nology taken in this chapter in part reflects the nature
of the endocrine system itself. The system’s most strik-

ing feature is its ability to coordinate extremely complex
interactions among its own disparate elements, the
rest of the body, and the external environment. Each
gland’s activity impinges on the others and on the body
as a whole. As textbooks of endocrinology despairingly
point out, it is artificial and misleading to depict the
development and nature of endocrinology in terms of
a particular disease, gland, hormone, or even a set of
interacting parts. The fact that often the peculiar mani-
festations of endocrine disorders initially drew attention
to the interrelationships of glands, hormones, nerves,
environment, and target cells underscores the impor-
tance of treating the history of research on the endo-
crine system in as holistic a manner as possible. !

The Enigmatic Glands

Like most other branches of science, endocrinology
has no obvious birthday to celebrate. Most of the
endocrine glands were discovered by the ‘kitchen
anatomy’ of hunters and cooks in prehistory or by
the medical anatomists of classical antiquity and the
Renaissance; a few — like the tiny parathyroids embed-
ded in the thyroid — were not found until the last
century. Similarly, ancient, medieval, and Renaissance
physicians noted several disorders — diabetes, goiter,
cretinism, dwarfism, and gigantism — which we now
know are caused by endocrine malfunction; but other
equally striking endocrine diseases were not described
until this century. And, whether by superstition or
empirical trials, physicians in many cultures and periods
have employed animals’ glands as drugs — precursors of
such modern glandular products as insulin and cortisone.
These early observations of anatomy, disease, and thera-
py were not linked together, however, until the latter
half of the nineteenth century and the beginning of the
twentieth. Only then did a combination of clinical
studies and the physiological experiments they generated
suggest that these mysterious glands had an important
role in the coordination of growth and metabolism.

It was well before the latter half of the nineteenth
century, however, that physicians and biologists began
to formulate the concept of animal hormones or internal
secretions. In 1766, for example, the celebrated Swiss

 
physiologist, Albrech von Haller, grouped together the
thyroid, spleen, and thymus because of their common
anatomical peculiarities — the lack of a secretory duct
and a plentiful supply of blood vessels — and suggested
that these “‘vascular glands’ poured special substances
directly into the veins and thus into the general circula-
tion. A few years later, in Recherches sur les maladies
chroniques, French physician Theophile de Bordeu
formulated a concept akin to what we now think of as
a hormone. De Bordeu speculated that “each organ of
the body gives off emanations which are necessary and
useful to the body as a whole,” and he particularly
stressed ‘‘the tonic effects of testicular and ovarian
emanations, and their influence on the secondary sex
characteristics as demonstrated by the obvious altera-
tions in the body in general which follow castration’
(Young 1970, p. 129, 130).

Thus, although the great French physiologist, Claude
Bernard, has often been credited with first formulating
the concept of internal secretion in the 1850s, the idea
that what we now call endocrine glands secrete sub-
stances into the circulation was current well before
Bernard's time. It is to Bernard, however, that we owe
the term “internal secretion,” and the first direct dem-
onstration of one internal secretion (the liberation of
glucose into the bloodstream by the liver) (Houssay
1967; Young 1970). Although Bernard's conception of
internal secretions, which included the possibility that
these substances might function to maintain the compo-
sition of the blood, was far broader than that later
formulated by endocrinologists, his preeminence in
nineteenth century physiology helped to focus attention
on the ductless glands.

It was in 1855, in a lecture at the Collége de France,
that Bernard discussed the liver’s internal secretion. The
same year, a book appeared that, perhaps more than
any other single work, deserves to be called the founda-
tion of modern endocrinology: Dr. Thomas Addison's
On the Constitutional and Local Effects of Disease of
the Supra-renal Capsules. Addison's work epitomizes
a sequence of observation and experiment that text-
books often call the ‘‘classic method” of endocrine
research, in which the clinical features of a disease were
compared and correlated with pathological changes in
a gland. Along with, or usually following, this study,
went observations on the effects of removing a gland
thought to be overactive, or, conversely, the effects
of administering an extract of a gland that was atrophied
or damaged.

Addison, a physician at Guy's Hospital in London,
was renowned in his own lifetime for his keen observa-
tions of his patients and his diagnostic skill. Comparably,
his monograph is such a descriptive masterpiece that
modern works on Addison's disease have not been able
to improve greatly upon its accuracy of detail (Hartman
and Brownell 1949, p. 343). From the study of only
eleven cases, Addison was able to pick out the ‘‘leading
and characteristic features of the morbid state.
anemia, general languor and debility, remarkable feeble-
ness of the heart's action, irritability of the stomach,
and a peculiar change of the color in the skin (Addison
1885, p. 214). Post-mortem examinations revealed a
diseased condition of the ‘supra-renal capsules,” as
Addison and earlier anatomists called the small pyramid-
shaped glands which sit on top of the kidneys. In some
of his cases the adrenals had been damaged by tubercu-
losis or cancer, but Addison could point to at least one
case in which the adrenals were the only abnormal
organs in an otherwise healthy body. This was good
evidence that the symptoms and condition he described
were, in fact, due to a malfunction of this gland alone
(Addison 1855, p. 210).

The monograph did more than describe a new disease,
however, for Addison saw clearly that his study of the
adrenals was a ‘‘first and feeble step towards inquiring
into the functions and influence of these organs’’ (Addi-
son 1855, p. 210). It seemed probable to him that the
general state of ignorance about the adrenals, as well
as the other ‘‘gland-like’’ organs, the spleen, thymus,
and thyroid, would be overcome by pathological studies
where physiological research had previously failed.
“Although pathology. .is necessarily founded on
physiology,” he wrote, “‘questions may, nevertheless,
arise regarding the true character of a structure or organ,
to which occasionally the pathologist may be able to
return a more satisfactory and decisive reply than the
physiologist” (Addison 1855, p. 209). Indeed, Addison
himself had “stumbled upon’ these ‘‘curious facts”
about the disease of the adrenals while searching for the
organic lesion of another mysterious disease, a fatal
anemia of unknown etiology. (His description in 1849
of this anemia, now known as pernicious anemia and
known to be caused by a vitamin deficiency, also is
classic.) Among his anemic patients, Addison had
noticed a few with a distinctive darkening or bronzing
of the skin, who at autopsy were found to have abnor-
mal adrenals. Addison was, of course, unable to say why
damage to the adrenal glands should alter the complex-

 
ion or cause a gradual, fatal debility. But, by directing
attention to the disease and the site of its lesion and
by emphasizing the utility of studying a diseased organ
to understand the functions of a healthy one, Addison
invited systematic research into the role of the ductless
glands in the general economy of the body.

Thirty years after Addison’s monograph, a French
physician, Pierre Marie, described and named another
remarkable malady, again exemplifying the early classic
method of endocrine research. In his 1866 paper, “Two
Cases of Acromegaly: An Unusual Hypertrophy of the
Head and Upper and Lower Extremities,”” Marie dis-
cussed two patients whom he had observed and another
seven cases he had found described in the medical
literature. He pointed out the excessive growth of the
viscera and the bones of the face, hands, and feet, and
the thickening of soft tissues like the tongue, lips,
and nose, which made the features of acromegalic
patients gradually become strikingly coarse and elon-
gated. Other signs and symptoms that Marie noted as
characteristic of the chronic condition included severe
headaches, intense thirst and appetite, cessation of
menstruation, changes in the thyroid, and damaged
vision. Later papers by Marie, his student Souza-Leite,
and other physicians added to the number of cases
and confirmed Marie's orginal description of the disease.

Marie hesitated in his first paper to offer an explana-
tion of the disease he had defined, because only one
autopsy had been performed. In that one case, published
a few years earlier by another physician, an egg-sized
tumor had been found in the brain “‘in the position of
the pituitary body’ (Marie 1886, p. 20). Marie consid-
ered this a lesion of the nervous system and thought
that the hypertrophy or enlargement of the pituitary
gland was suggestive of the hypertrophy of the bones
of the face and extremities. But, he carefully added, the
two might have had no cause and effect relationship —
this was only one of several plausible hypotheses about
the cause of acromegaly. Marie's reluctance to seize
upon the abnormality of the pituitary gland as the pri-
mary cause of acromegaly may also have been influenced
by the prevalent belief among physiologists that this
gland had “little, or perhaps no, use in the organisms of
the higher vertebrates” (Rolleston 1936, p. 55). But
Marie's clear account of the syndrome, even without
speculations about its cause, encouraged others to search
the literature, clinics, and anatomical museums for
further examples. Two years after Marie's first paper,
Otto Minkowski — more famous for his work on the

pancreas and diabetes — explicitly made the connection
between acromegaly and a disease of the pituitary gland.
Then, in 1890 and 1891, Marie reported that enlarged
pituitaries always were found in post-mortem examina-
tions of persons with acromegaly, and he hypothesized
that the abnormal growth of the pituitary caused a
glandular deficiency and hence toxemia (Rolleston
1936, p. 86).

By implicating a particular gland in a specific disease,
Addison and Marie gave physicians and physiologists
both a reason and a method for studying the ductless
glands. Over the centuries, as we have indicated, there
had been occasional attempts to see what happened
when a gland was removed or transplanted, but no one
had followed up on them seriously. The well-known
effects of castration on men and animals, for example,
had led the eighteenth century surgeon, John Hunter,
to try transplantation experiments with the gonads and
accessory sex organs of hens and roosters. In 1849
similar experiments were carried out by the German
physician, A. A. Berthold, out of a particular interest
in the structural changes in the transplanted gonads and
a general interest in the nature of sex, heredity, and the
“sympathies’”’ between different parts of the body
(Jdrgensen 1971, pp. 27-30). Astley Cooper and T. W.
King tried removing the thyroids of dogs in the 1820s
and 30s and suggested that the thyroid might form some
“particular material’’ which exerted an influence ‘upon
the circulating fluid [which] may be more or less need-
ful for the healthy subsistence of the entire animal”
(Rolleston 1936, pp. 18, 50). Addison's monograph
immediately inspired the French physiologist, Brown-
Séquard, and others to do systematic extirpation experi-
ments on the adrenals, with contradictory results.
Brown-Séquard believed that the adrenals were necessary
to life because he found that the removal of both
adrenals from various animals was always fatal; Philli-
peaux, on the other hand, was able to excise the adrenals
and other glands from white rats without killing them.
The different results were due partly to different surgical
techniques and precautions against infection and partly
to the existence of unnoticed accessory adrenals in
white rats which enabled them to survive the loss of the
main pair, as well as differences in resistance to stress
and infection among different strains of animals. Similar
debates over the indispensability of the pituitary and the
thyroid glands took place in the 1880s.

The variable results of extirpation experiments
underscores the importance of surgical and aseptic

 
techniques for the development of endocrinology. When
Emil Theodor Kocher received the Nobel Prize in
Medicine in 1909 for his work on thyroid diseases, he
began his lecture by exalting Pasteur’s discoveries in
bacteriology and Lister's application of them to surigical
practice. Thanks to aseptic procedures, Kocher empha-
sized, it at last was possible for surgeons and physiolo-
gists to ‘make all the organs accessible to direct observa-
tion, and to alter the conditions in which they exercise
their functions (Kocher 1909, pp. 330-33). Surgical
technique, too, often meant the difference between a
clearcut and an inconclusive experiment. The results
of thyroid extirpation had been complicated by the
failure to recognize and leave intact the tiny parathyroid
glands in the midst of the thyroid tissue; the effects of
removing the pituitary gland were confused by the
effects of surgical damage to the hypothalamic region
of the brain.?

Perhaps the most celebrated example of the impor-
tance of surgical skill for the development of endocri-
nology is Minkowski’s discovery of the role of the
pancreas in diabetes in 1889. The physician von Mering
was studying the problem of fat absorption in diseases
of the pancreas and wanted to know how the decreased
secretion of pancreatic juices into the intestine affected
the breakdown of fats. When Minkowski asked why he
did not remove the pancreas, von Mering answered that
this was impossible. Minkowski, proud of his surgical
skill, replied brashly, “Why should it be impossible?
Bring me a dog and | will remove the pancreas.” The
operation succeeded, but to Minkowski’s annoyance
the supposedly well-trained dog began urinating fre-
quently and copiously. On an impulse, or at the sugges-
tion of his chief, von Naunyn — stories differ — Minkow-
ski collected some of the urine from the floor and tested
it for sugar. The sugar content was surprisingly high, a
familiar sign of diabetes mellitus. After a week of
further operations on other dogs, Minkowski was able
to tell von Mering that total removal of the pancreas
resulted in diabetes mellitus (Nothman 1954, pp. 272-
274; Allen et al. 1919, p. 38; Young 1970, pp. 137-140).

Surgical skill and asepsis also helped to decide be-
tween two competing theories of the function of the
ductless glands. The first of these theories, widely held
in the late nineteenth century and well into the first
two decades of the twentieth, was that these glands
somehow neutralized or removed poisons in the blood;
consequently, disease or removal of these organs caused
toxemia. It is easy to see in this theory the strong

56

influence of bacteriological and immunological modes of
explanation current at the time. However, the alternative
explanation, that the glands secreted necessary sub-
stances into the bloodstream, had a long history of
illustrious proponents such as von Haller. Cooper and
King’s experiments in thyroid removal in the 1820 and
30s, as we have seen, led them to this thesis: that glands
such as the thyroid released a special substance directly
into the blood. In the 1840s George Gulliver, surgeon
and Fellow of the Royal Society, reported that under
the microscope spheroidal bodies could be seen in both
the adrenals and the veins leading from them; he argued
that the veins served as the duct for some ‘‘peculiar
matter which doubtless had some special use’” and
which was produced by the adrenals. Gulliver considered
this “‘an interesting and important subject for further
inquiry,” but neither he nor anyone else pursued it at
the time. Like many other early examples of the internal
secretion hypothesis, this work was ignored until the
hypothesis was firmly established and its history began
to be written (Rolleston 1936, pp. 18-20).

The first good evidence for the internal secretion
explanation of the glands’ function came through
research on thyroid diseases and the unhappy results of
thyroid surgery on humans in the 1870s and 80s. In
England W. W. Gull and W. M. Ord described a condition
which Ord called myxedema: a swelling of the face and
body from an excess of a gelatinous substance, mucin,
accompanied by impairment of the mental faculties,
lethargy, and extreme sensitivity to cold. In its advanced
stages, myxedema strongly resembled cretinism. Cretin-
ism, in turn, was associated with thyroid abnormalities
but in very confusing ways; many victims of “endemic
cretinism’’ had immense goiters, while cases of ‘sporadic
cretinism’’ generally had tiny atrophied thyroids. Ord
noted that in all five of his cases of myxedema the
thyroid was small, but he thought it had simply been
squeezed by the excess mucin. In Switzerland, mean-
while, where goiter was especially common, removal
of the grossly enlarged thyroids became popular once
the antiseptic method made such surgery a less danger-
ous affair. Unfortunately, some patients whose goiters
had been removed began to suffer a new malady which
was variously ascribed to injury of the nerves or trachea
or to loss of some “blood-making’”’ function of the
gland.

In both England and Switzerland a few bold physi-
cians speculated that all three conditions — sporadic
cretinism, myxedema, and the illness that followed
thyroid operations — resulted from the absence or
degeneration of the thyroid. Schiff, who had done
experimental thyroidectomies on animals thirty years
earlier and thought then that the thyroid produced an

internal secretion, now saw the clinical significance of

his earlier research; he tried implanting thyroids into
the abdomens of thyroidectomized animals and suc-
ceeded in preventing myxedema. At this point it was
clear that the thyroid was necessary for health, but
the blood detoxification hypothesis was still tenable.
Then, in 1891, George Murray described his successful
attempt to treat human myxedema with extracts of
sheep thyroid glands; and three years later, Magnus-Levy
showed that such extracts speeded up metabolism. Thus,
the thyroid and its secretion gradually was recognized
as having an active function unrelated to detoxifying
the blood but indispensable to health (Paget 1919,
pp. 54-67; Rolleston 1936, pp. 29-30, 151-153).

The discovery that thyroid extracts or grafts could
restore normal intelligence and vigor to the myxedema-
tous patient attracted a great deal of both scientific and
popular attention, for it showed that a disease could
be caused by an insufficiency of the secretion of a duct-
less gland and, in turn, that the symptoms of such a
disease could be cured by what was termed replacement
or substitution therapy. The interest caused by clinical
studies of the thyroid gland, however, was overshadowed
by more sensational claims for the actions of internal
secretions, associated with the theories and activities
of Charles-Edouard Brown-Séquard.

In retrospect, Brown-Séquard has been recognized as
“a remarkable pioneer in endocrinology,” whose thera-
peutic studies, ‘although they later fell into disrepute,
sparked the imagination of many investigators [and] led
to an active search for ‘internal secretions’ in animal
tissues’ (Rolleston 1937, p. 261; Borell 1975, p. 1).
Elected to England's Royal Society and France's Acade-
mie des Sciences, Brown-Séquard’s peripatetic career
saw him practicing medicine, teaching, and doing re-
search in locales such as Paris, Boston, New York,
Philadelphia, London, and Dublin.

Addison's book on the symptoms of adrenal insuf-
ficiency, as we noted, sparked Brown-Séquard’s interest
in the ductless glands, and in 1856 he concluded that the
adrenals are essential to life after performing total
adrenalectomies on dogs. In his 1869 course of lectures
at the Paris Faculty of Medicine he set aside his earlier
views about the detoxifying function of the adrenals in
favor of the theory that the ‘glands have internal

57

secretions and furnish to the blood useful if not essential
principles’”’ (Major 1943, p. 375). Then, in 1889, after
he had succeeded Claude Bernard as professor of medi-
cine at the Collége de France, Brown-Séquard reported
to the Society of Biology that, in experiments per-
formed on himself, he had shown the rejuvenating
effects of testicular extracts from healthy young guinea
pigs. Between 1889 and his death in 1894, Brown-
Séquard and his assistant, d’Arsonval, extended their
investigations to include the therapeutic effects of
extracts from other animal tissues, based on Brown-
Séquard’s expanded concept of internal secretions.
Every tissue of the organism, he postulated, secretes
its own special product into the blood and this influ-
ences ‘‘all other cells which in this way are dependent
on each other, by a mechanism different from the
nervous system’’ (Houssay 1967, p. 165; Brown-Séquard
1889, pp. 415-422).

To the world at large, including many physicians,
the details of Brown-Séquard’s concept were far less
exciting than the therapeutic possibilities it implied;
by 1890, an estimated 12,000 physicians were giving
testicular extracts to their patients, despite the skepti-
cism and embarrassment expressed by many medical
journals (Olmsted 1964, pp. 209-211).

Brown-Séquard, too, was concerned about the
sensational publicity that his experiments received, and
angered at the lucrative business of glandular extracts
engaged in by some physicians. Nonetheless, he believed
strongly that his experiments with testicular and other
extracts were premised on sound physiological thinking,
and would open up a new realm of therapeutics.

. .now we believe that all the tissues, glandular
or not, give something special to the blood, that
every act of nutrition is accompanied by an inter-
nal secretion. We believe, in consequence, that all
the tissues will be able to be and ought to be em-
ployed in special cases as a mode of treatment;
that there is, in short, a new therapeutics to create,
in which the medicaments will be products pro-
duced by the different tissues of the organism.

The bacterial products taught us how active the
chemical compounds created by the infinitely
small were: the living cell, of each tissue that
belongs to the organism, must, by analogy, secrete
some products, of which the efficacy is no less.
(Brown-Séquard and d’Arsonval 1891; trans.
Borell 1975, pp. 3-4)
’

The therapeutic movement called ‘‘organotherapy,’
sparked in large part of Brown-Séquard’s work, was a
flamboyant, controversial chapter in the history of
endocrinology, one that many later endocrinologists
would have preferred to ignore because of the cloud
that it cast over clinical endocrinology. The editor of
the British Medical Journal in 1937, for example, wrote
of the organotherapy movement as follows:

After the discovery that preparations of thyroid
gland taken by mouth were of benefit in myx-
oedema and cretinism, thyroid extract began to
be given for many and varied conditions, and
extracts of other ductless glands were prescribed
with an enthusiasm that outran knowledge.
Indiscriminate endocrine therapy brought about
the inevitable reaction, and clinical endocrinology
came to be looked upon with suspicion. The
intensive research work carried out over the past
decade has gone far to remove the disfavour into
which endocrinology had fallen, and it is now
becoming possible to put the matter in some kind
of perspective. Solid achievements have been
made. Possibilities are daily becoming probabili-
ties. But the exploitation of these probabilities
in the interest of the patient must be carried out
with due caution and a healthy skepticism if
endocrinoloby is not to be done at the disservice
of again becoming a fashion. (The Endocrines in
Theory and Practice 1937, Preface)

Despite the negative effects of the excesses com-
mitted in the name of organotherapy, however, the
movement was a positive force for the development of
endocrinology in other respects. Fo:, as historian of
endocrinology Merriley Borell points out, “much was
learned about the action of internal secretions by means
of these therapeutic efforts. The organotherapy effort
was fundamental in attracting the attention of scientists
to the field, who then sought to set up standards for the
proper investigation of these therapeutic effects. Here,
clearly, clinical concerns pointed the way to new scien-
tific problems” (Borell, personal communication).

One such route was followed by the British physician
George Oliver, who experimented with extracts of vari-
ous tissues, including the adrenal and thyroid glands and
the brain. Oliver had been administering extracts to his
son, and then using an instrument he had developed
to measure their effects on the diameter of his son's
radial artery. In 1893, he observed that adrenal extracts

ee

58

from sheep and calves caused a sudden rise ‘in blood
pressure, while other glandular extracts generally low-
ered it. Oliver took his adrenal extract to E. A. Schafer,
professor of physiology at University College, London,
and caught him — so tradition has it — at a moment
when he was measuring the blood pressure of an anaes-
thetized dog. Schafer was dubious about Oliver's claim,
but agreed to inject some of the extract into the animal's
veins. To Schafer’s astonishment, the mercury in the
blood-pressure manometer shot up so quickly and so
high that the recording float was nearly lifted out of
the tube (Dale 1938, pp. 461-463; Barcroft and Talbot
1968, pp. 6-8). Oliver and Schafer’s studies of this
pressor effect of adrenal extract not only led to the
first isolation of a hormone (epinephrine), but also to
a better understanding of the physiological role of the
glands of internal secretion.

The arguments over the possible blood detoxifying
function of the adrenals subsided once the definite,
measurable effect on blood pressure was demonstrated.
Oliver and Schafer also correlated function with anat-
omy; they showed that extracts made from the inner
part of the adrenals, the adrenal medulla, would raise
blood pressure, while extracts from the outer layer, the
cortex, were ineffective (Rolleston 1936, pp. 29, 331).
Research into the physiological implications of anatom-
ical distinctions between parts of other glands, such as
the anterior and posterior lobes of the pituitary, and the
islets of Langerhans in the pancreas, quickly followed
and proved fruitful. The fact that the internal secretion
of a gland might actually contain several different active
substances, each produced by a particular kind of tissue
or cell, was at first confusing but later became axio-
matic, and helped to direct attention to the complicated
interactions of hormones and glands. Finally, the isola-
tion of the pressor substance from the adrenal medulla
at the end of the nineteenth century and its crystalliza-
tion as a pure compound by Jokichi Takamine and T. B.
Aldrich (working independently) in 1901 demonstrated
concretely the existence of an internal secretion, and
enabled scientists to study the pressor effect and other
characteristic actions of epinephrine in much more
carefully controlled experimental situations (Marti-
Ibanez 1952, p. 233).

When Oliver and Schafer first reported their study of
the pressor effects of adrenal extract to the Physiological
Society in March 1894, their audience included two
young investigators in Schafer’s laboratory, William
Bayliss and Ernest Starling. In 1902, investigating the
control of pancreatic secretions, Bayliss and Starling
identified a new internal secretion that they named
secretin. Their discovery was made when they attempted
to pinpoint the pathway of the neural reflex that the
Russian physiologist, Ivan Pavlov, had declared must
be responsible for the flow of pancreatic secretions into
the intestine to neutralize digestive acids. Bayliss and
Starling, however, found that even when all the nerves
between the small intestine and the pancreas were sev-
ered, acid in the duodenum would still provoke the flow
of pancreatic juices. According to C. J. Martin, who was
present when the experiment was performed, Starling
concluded at once, “Then it must be a chemical reflex.”
He promptly made a crude extract from a piece of
duodenum, injected it into the jugular vein of the dog,
and within a few moments had the pleasure of seeing
the pancreas respond with a heavy secretion (Barrington
1975, p. 11).

Starling used the occasion of the Croonian Lectures
‘to the Royal College of Physicians of London in 1905 to
bring together what was known about ‘‘the chemical
correlation of the functions of the body.” In these
lectures he introduced the word ‘hormone’ (from the
Greek, hormao, to excite or arouse to action) for the
general class of substances ‘‘which, speeding from
cell to cell along the blood stream,. . .coordinate the
activities and growth of different parts of the body’
(Starling 1905, p. 340). As examples of these chemical
messengers, he named epinephrine, secretin and a
number of similar gastric hormones which had been
discovered in the meantime, extracts from the thyroid
and from the interstitial cells of the testes and ovary,
and — more tentatively — the supposed internal secre-
tion of the pancreas. The simplicity and convenience
of the word “hormone” soon made it popular even
though, as etymological and physiological purists point-
ed out, it applied to substances which could inhibit
activity as well as excite it. The words ‘endocrine’
and “endocrinology,” (from the Greek, | separate
within) came into use about half a dozen years later
(Rolleston 1936, pp. 2-4).

Interrelationships Among the Endocrine Glands

Building upon the observations and clinical studies
of physicians, the discovery of secretin in 1902 and
Starlings elaboration of the hormone concept in 1905
represent a watershed in the emergence of endocrinology
as a field of basic as well as clinical research. In the case
of the thyroid, adrenals, and the duodenal extract

named secretin, physicians and physiologists had suc-
ceeded in their effort to confirm the long-presumed
existence of potent secretions in animal tissues. That
proof came both from the ability of glandular extracts
to cure specific diseases such as myxedema and from the
analysis of specific physiological responses to the chemi-
cal substances in adrenal and duodenal extracts.

When secretin was discovered, as Borell observes,
the term “‘internal secretion” ‘no longer provided an
adequate description of the phenomenon under study.
It did not specify the messenger role, the activity poten-
tial of chemicals elaborated by certain tissues,” as did
the word ‘hormone’ (Borell 1975, p. 8). And, as
Starling and other investigators recognized at the turn of
the century, the chemical coordination of physiological
processes by hormones was now a major subject for
biological research, one that seemed of equal import
to understanding the integrative action of the nervous
system. For, as Starling wrote in Lancet in August 1905:

oa

If control of the different functions of the body
be largely determined by the production of defi-
nite chemical substances within the body, the
discovery of the nature of these substances will
enable us to interpose at any desired phase in
these functions and so to acquire an absolute
control over the workings of the human body.
Such a control is the goal of medical science.
(Maisel 1965, p. ix)

Building upon the idea of a human control of physio-
logical processes, the next phase of research in endocri-
nology began to delineate and emphasize the intricate
functional interactions among the glands. The early
endocrinologists had tacitly assumed that each gland
produced its own special hormone and had its own
particular effect on the body, and endocrine diseases
thus were viewed as the consequence of an increase
or decrease in the secretion of a hormone. By the 1920s,
however, closer study of endocrine diseases coupled with
animal experimentation made endocrinologists see that
this picture of the endocrine system was greatly over-
simplified. The central fact — and the central problem —
of endocrinology between the World Wars was that
activities of one gland could control and be controlled
by the activities of others.

Research now concentrated on pairs or groups of
glands, and the choice of which constellation of glands
to study was still largely determined by clinical data and
interests. The sexual abnormalities found in many

 
endocrine disorders, the association of diabetes and
acromegaly, the enlarged adrenals common to many
different illnesses, the apparent therapeutic value of
“pluriglandular’’ preparations, the ability of epinephrine
to alleviate but not to cure Addison's disease — each of
these clinical observations led to new insights into the
complexities of metabolism and to new approaches to
therapy.

Three areas of research, moving back and forth
from the clinic to the laboratory, proved especially
successful and fruitful in this period. First, in the lineage
begun by Thomas Addison, there was a body of work on
the adrenals by Cannon, Selye, von Euler, Kendall,
Moore, and many others. Their researches, in brief
synopsis, helped to elucidate the roles of the two layers
of the adrenal — the medulla and the cortex — in main-
taining homeostasis and coordinating the body's re-
sponse to emergencies and stress; established the nature
of the medulla’s close connections to the sympathetic
nervous system; provided a better understanding of
the relationships between the pituitary gland and the
adrenal cortex; and identified, isolated, purified, and
ultimately synthesized ACTH, the pituitary gland
hormone which stimulates the adrenal cortex, and
the several hormones secreted by the adrenal’s two
layers.

Secondly, there was a focus of research on the
endocrinology of sex and reproduction. Work in this
area received a powerful stimulus from the joint decision
of the Bureau of Social Hygiene, the National Research
Council, and the Rockefeller Foundation in 1921 to
support ‘‘a program of research on fundamental prob-
lems of sex,” and in 1931 to sponsor a major survey of
sexual endocrinology: Sex and Internal Secretions.
This review of the recent progress in the biology of
sex and the sex glands, first published in 1932, attracted
many new workers into the field (Young and Corner
1961, |, ix-xii; Hall, work in progress).

A third major area of research, dealing with the
functions of the pituitary gland and, in particular, the
relations between pituitary disorders and diabetes,
culminated in establishing for a time a view of the
anterior pituitary as ‘‘the master gland’ or “conductor
of the glandular orchestra.” The methods shared by all
three areas of research included not only the familiar
techniques of extirpation and replacement by trans-
plants and extracts, but also the use of isolated and
purified hormones like thyroxin and insulin as these

became available, and comparative studies of the endo-
crinology of other species.

In the remainder of this section, we will illustrate
the nature of this second phase in the development
of endocrinology by highlighting research on the pitui-
tary gland or hypophysis, physiologically the most
complex and important of the ductless glands. About
1890, as we have seen, Marie, Minkowski, and others
explained the condition of acromegaly in terms of a
lesion of the hypophysis which decreased the gland’s
internal secretion. Five years later, in the course of
their experiments on the dramatic power of adrenal
extracts to raise blood pressure, Oliver and Schafer
discovered that hypophyseal extracts also had a pressor
effect. The hypophysis, like the adrenals, has two
anatomically distinct parts: the anterior lobe or ade-
nohypophysis and the posterior lobe or neurohypo-
physis. By 1898, Howell and Schafer and Vincent had
shown that only extracts of the posterior lobe exerted
a pressor effect, and so research centered on this lobe
of the gland for many years. During the first decade
of the twentieth century, a bewildering array of specific
effects were attributed to the posterior lobe. While an
extract of the posterior lobe as a whole increased blood
pressure, one fraction of it had the opposite effect
of lowering blood pressure. The extract produced in-
tense contractions of the uterus and weaker contractions
in some other plain muscles. It provoked the secretion
of urine almost immediately, but this diuretic effect
soon gave way to an even stronger antidiuretic effect.
In some mammals posterior lobe extracts made milk
flow more easily and in greater amounts than usual.
In frogs the posterior lobe seemed to control the con-
traction and expansion of the pigments cells and thus
the color of the frog's skin (Sharpey-Schafer 1924-26,
11, pp. 252-257).

These varied effects of posterior lobe extracts were
both interesting and useful. The uterine contraction re-
sponse provided a quantitative bioassay for the potency
of posterior lobe extracts and found an application in
obstetrical practice. The antidiuretic effect was first dis-
covered when patients with diabetes insipidius — a form
of diabetes characterized by a great flow of dilute urine
and a correspondingly great thirst — were relieved by ex-
perimental injections of pituitary extract; this quickly be-
came a standard treatment of the disease (Sharpey-Sha-
fer 1924-26, 11, p. 244). But none of the actions of the
posterior lobe of the pituitary could explain acromegaly.

 
As the American neurosurgeon Harvey Cushing wrote
eloquently, the great difficult for all pituitary gland
researchers was getting at the gland in the first place.

Nature saw fit to enclose the central nervous
system in a bony case lined by a tough protecting
membrane, and within this case she concealed a
tiny organ which lies enveloped by an additional
bony capsule and membrane like the nugget in the
innermost of a series of Chinese boxes. No other
single structure is so doubly protected, so centrally
placed, so well-hidden. (Cushing 1930, p. 5)

In 1904 Cushing forecast that techniques of brain
surgery were improving so much that “‘it is not impos-
sible that a diseased pituitary may someday be success-
fully attacked’ (Fulton 1946, p. 267). Only two years
later the British surgeon, Victor Horsley, successfully
operated on several cases of pituitary tumors (Paget
1919, p. 180). Soon Cushing too was actively engaged
in pituitary gland surgery and research.

Cushing had been interested in the hypophysis ever
since 1901 when he had failed to recognize that a case
of sexual infantilism accompanied by obesity, headache,
retarded growth, and impaired vision was a case of
pituitary tumor. His pride was nettled because, soon
after finding the tumor at autopsy, he learned that A.
Frohlich in Vienna had seen a similar case, made the
correct diagnosis, and had the tumor removed success-
fully (Fulton 1946, pp. 271-272). In 1907-1908 Cush-
ing’s interest was renewed by the announcement of a
new technique for removing the gland from dogs and by
a series of lectures on the pituitary that Schafer deliv-
ered at John Hopkins. Cushing and his students at Johns
Hopkins then began a long series of pituitary gland
extirpation experiments on dogs, correlating the results
with the conditions he found in his patients.

Cushing's chagrin over his misdiagnosis of what
came to be called ““Frohlich’s syndome’’ was redeemed
by the first major resuit of these experiments. Earlier
reports on removal of the gland said that the animals
always died after the operation. Some of Cushing's
dogs, however, survived the surgery and lived many
months although they became “extraordinarily fat,
logy, sexless creature(s).”” The general opinion among
Cushing's students was that somehow the operation had
not been complete, but they drew no further conclu-
sions from the peculiar state of the animals. One day
in the winter of 1908-1909 Cushing “‘caught sight of
[one of] these animals while it was still alive and said

at once, ‘Here is Frohlich’s asexual adiposity.” ’ Because
the animals lack all or nearly all of the pituitary, Cushing
deduced that Frohlich’s syndrome must be caused by a
lack of the pituitary secretion. Moreover, if this state of
asexual adiposity was the result of too little pituitary
secretion, then acromegaly must be the result of an
excessive secretion — exactly the reverse of Marie's
original explanation of acromegaly (Fulton 1946, pp.
280-282).

Over the next four years, Cushing confirmed his
deductions in further experiments and studies of pa-
tients with a variety of pituitary gland disorders. He
demonstrated that under- or over-secretion by the
anterior lobe alone was responsible for Frohlich’s
syndrome and acromegaly, as well as for gigantism and
a form of dwarfism. He also stressed the effects that
pituitary lesions had on the rest of the endocrine system:

In view of the apparent interrelation of many of
the glands of internal secretion it is quite probable
that certain of the symptoms known to accom-
pany hypophyseal disease may be consequent
upon a secondary change in other glands which
follow the primary change of the hypophysis.
These changes are seemingly more outspoken and
more widespread after a lesion of the pituitary
body than after a corresponding lesion of any
other member of the group of ductless glands,
and in view of its unusually well-protected posi-
tion one might have conjectured that it must rep-
resent a vitally important organ. (Fulton 1946,
p. 301)

Cushing's strong awareness of the secondary endo-
crine effects of hypophyseal disorders led twenty years
later to his elucidation of what had been vaguely known
as “‘polyglandular syndrome’ and usually ascribed to a
malfunction of the adrenal cortex. In acromegaly he
had noted in the anterior lobe a preponderance of cells
which take up eosin dyes, and he concluded that acro-
megaly was due to oversecretion by these eosinophilic
cells. At the same time he argued that oversecretion by
the other distinctively staining cells of the anterior lobe,
the basophiles, must also be responsible for some kind
of syndrome, even though he could not say what that
syndrome was. In 1930 he read of a case of “‘adiposital-
genital dystrophy’ which at autopsy revealed a tiny
adenoma (tumor) of the basophilic cells. The case
resembled in every detail cases of ‘‘polyglandular syn-
drome’ he had seen over the years, and further post-

 
mortem evidence of basophilic tumors confirmed
the matter. By comparing the characteristic features of
acromegaly and polyglandular syndrome, Cushing had
long ago concluded that the eosinophilic cells secreted a
hormone which regulated growth. Now he could add
that the basophilic cells elaborated ‘‘a sex-maturing
principle” or “a gonad-stimulating factor’’ (Cushing
1932, pp. 114-119, 155-161; Fulton 1946, pp. 614-
616).

Inevitably, the situation turned out to be more
complex than Cushing's account in 1932 made it appear.
More sophisticated cell staining techniques revealed
many specialized cell types within the general categories
of eosinophile and basophile. Moreover, the original
explanation of the polyglandular syndrome (since
renamed ‘‘Cushing’s syndrome’’) in terms of an adrenal
cortex disorder was vindicated: excessive production of
the steroids of the adrenal cortex was the immediate
cause of the symptoms of the disease, although such
hypersecretion of steroids was often in turn the result of
oversecretion of ACTH by the anterior pituitary. How-
ever, the main outlines of Cushing’s explanation of the
syndrome and his characterization of a growth factor
and a gonad- stimulating factor proved to be sound.

Concurrent research by Bernardo Houssay in Argen-
tina and by Herbert McLean Evans at Berkeley did much
to confirm and extend Cushing's clinical insights into the
workings of the anterior lobe and its ties to other
endocrine glands. In 1907, the year that Cushing began
his extensive work on the hypophysis, a precocious
young medical student in Buenos Aires saw a patient
with acromegaly and immediately became interested
in the gland. Forty years later, in his Nobel Prize lecture,
Bernardo A. Houssay commented that he had been
attracted to the hypophysis by both its medical and
physiological aspects: ‘“the microscopic picture showed
glandular activity and its lesions were accompanied by
serious organic disturbances, such as acromegaly, dwarf-
ism, etc.” (Houssay 1947, p. 211; Young and Foglia
1974, p. 254). Beginning with his medical thesis in 1911,
and continuing through a long series of researches,
Houssay developed techniques for removing the hypo-
physis from frogs, toads, and dogs, and examined the
physiological effects of posterior lobe extracts and
implants on muscles, the uterus, carbohydrate metabo-
lism, the thyroid, and the adrenals.

Houssay’s most important research in endocrinology
began after Banting and Best announced the discovery
of insulin in 1921, a year that Houssay later saw as a

critical year for endocrinological research and thinking.
The secretion of insulin by the islets of Langerhans had
been predicted years before Banting and Best succeeded
in extracting it from the pancreas, but with insulin’s
existence proven in 1921, no one could doubt any
longer the existence of hormones or their ability to
regulate metabolism. Moreover, as the association be-
tween acromegaly and diabetes had been noted often by
clinicians, Houssay saw that insulin could serve as a new
tool for investigating the suspected physiological reac-
tions between the hypophysis and the pancreas (Houssay
1956, p. 213; 1967, pp. 167-168).

Houssay had to devote several years to the prepara-
tion and standardization of insulin for his experiments,
for large-scale extraction of insulin for treatment began
only in 1923-1924, and pure crystalline insulin was not
prepared until 1926. He and Magenta demonstrated in
1924 that a dog without its hypophysis became remark-
ably sensitive to insulin’s ability to lower blood sugar
levels. It was not clear from their experiments, however,
whether it was the loss of the anterior lobe or of the
posterior lobe that was responsible for this hypoglyce-
mic effect. Until 1929 the general opinion was that “if
the hypophysis had any action on carbohydrate metabo-
lism and on the diabetes of acromegaly it was due to its
posterior lobe” (Houssay 1943, p. 247). The anterior
lobe was ignored by researchers because the actions of
its extract seemed to be transient and because it was
hard to extirpate the lobe surgically (Houssay 1956,
p. 213).

Houssay’s early studies of the hypophysis in am-
phibians, dogs, and man proved their value in 1929
when he realized that the anatomy of the toad’s pitui-
tary made it the ideal experimental animal for testing
these widely-held views of the pituitary’s role in carbo-
hydrate metabolism. Houssay found that removing the
lobe which corresponds to the anterior lobe in man
produced great sensitivity to insulin, while removal of
the posterior lobe had no such effect. Without the
anterior lobe, the toad rapidly used up glucose, and the
injection of insulin exacerbated this high rate of sugar
utilization. Thus the anterior lobe clearly was implicated
in the regulation of carbohydrate metabolism (Houssay
1936 a, b). The diabetic’s problem, though, was that his
body used sugar too slowly. Houssay and Biasotti proved
in 1929-1930 that the effect of the anterior pituitary
on glucose metabolism was antagonistic to the effect of
the pancreas. If a toad or dog was made diabetic by the
removal of its pancreas, the removal of its anterior lobe

 
would then counteract the diabetes. If, on the other
hand, the animal was made mildly diabetic by the
partial removal of its pancreas, an injection of anterior
pituitary extract would drastically increase the severity
of the diabetes. While the pancreas secreted insulin to
increase the utilization rate of sugar, the anterior pitui-
tary secreted something with the opposite effect, some-
thing which inhibited the supply of sugar.

These experiments and results were not well under-
stood or accepted in the early 1930s, both because
Houssay published them in Spanish-language journals, and
because they contradicted the current theories of
hypophyseal function so completely that journals in the
U. S. would not publish his English summaries. One
distinguished physiologist declared that Houssay had to
be wrong because it was well-known that the posterior
lobe’s primary function was metabolic control (Barring-
ton 1975, p. 54; Young and Foglia 1974, p. 256). In
addition, others who tried to reproduce the experiments
failed, chiefly because they did not follow Houssay's
techniques for preserving the activity of pituitary
extracts (Houssay 1943, p. 252; Wrenshall et al. 1962,
p. 65). Eventually, however, the “diabetogenic’’ effect
of the anterior lobe in mammals was confirmed in
1931-1932 through the researches of Herbert McLean
Evans and Miriam Simpson, who had been working with
anterior lobe extracts from a very different point of
view.

Evans and Simpson observed the diabetogenic effect
in the course of a wide-ranging program of basic research
on the effects of the anterior pituitary extracts on
growth and reproduction, work which in turn fed
back into clinical aspects of endocrine disorders through
the type of feedback cycle so characteristic of the
development of endocrinology (Evans 1923-24). In the
midst of their efforts to isolate and purify the growth
hormone (a task achieved in 1944-45), Evans and
Simpson noticed in 1931 that one of their dogs in which
gigantism had been induced with the growth hormone
ate and drank excessively, yet became thin and weak.
The dog also “excreted great amounts of urine to which
flies were attracted.” Like Minkowski in 1889 (and
Evans, who was very interested in history of science,
surely knew the anecdotes about Minkowski’s discov-
ery), Evans and Simpson tested the urine and blood for
sugar and found that the dog was suffering from diabe-
tes. The experiments proceeding from that observation
gave the first clear evidence that the anterior lobe pro-
duced an antagonist to insulin and reassured Houssay

that his remarkable results with amphibians were correct
(Amoroso and Corner 1972, pp. 128-129).°

By the mid-1930s, then, there were strong medical
and experimental reasons for believing that the anterior
lobe was, as Houssay put it, “the central and directing
organ in the endocrine constellation” (Houssay 1936
b, p. 961). Little over a decade later, concentrated
research in biochemistry had proven that the gland’s
control of growth, reproduction, metabolism, and the
activities of other endocrine organs was carried out
through the secretion of six different hormones, and all
six hormones were purified by 1950. However, immedi-
ately after proclaiming the central importance of the
anterior lobe in his Dunham Lectures at Harvard in
1935, Houssay was forced to add that the other endo-
crine organs ‘‘in some. . .cases. . .also have an influence
on the pituitary’ (Houssay 1936 b, p. 961). Intensive
research into the reciprocal influences of the endocrine
glands and the hypophysis on rates of internal secretion
kept pace with identification and purification of the
anterior lobe’s trophic hormones through the 1930s and
40s. The general conviction of the early 1920s that the
endocrine organs did not act independently — an opin-
ion based primarily on clinical data — now rested on the
solid ground of physiological and biochemical experi-
mentation, and the availability of newly purified hor-
mones gave hope that many more of the complex inter-
actions would be successfully untangled in the future.

The Rise of Neuroendocrinology

Between the World Wars endocrinology became
firmly established as a scientific discipline with a distinct
perspective of its own towards physiological problems.
Endocrinologists regarded the endocrine glands, hor-
mones, and their interactions under the pituitary gland’s
direction as the body's long-term system for coordinat-
ing and regulating its activities, a system that neatly
complemented the more rapid integrative functions of
the nervous system. Most endocrinologists would have
described the two systems as separate but equal, al-
though some enthusiasts claimed that the glands con-
trolled the brain and nerves (Vincent 1925, pp. 11, 18;
Rolleston 1936, pp. 57-9; Liljestrand 1936, p. 398;
Berman 1930, pp. 200-218). For some time, though,
evidence had been building up in a variety of fields —
human pathology, psychology and psychiatry, compara-
tive anatomy, experimental physiology and endocrinol-
ogy, and animal behavior — to suggest that, once again,
the picture was more complicated than either the

 
endocrinologists or the neurophysiologists realized.
The nervous system and endocrine system were not
independent modes of internal communication after
all, but interconnected in very interesting ways.

Out of the study of these interconnections a new
hybrid discipline, neuroendocrinology, emerged in the
1940s and 50s. Early clues to a relationship between the
endocrine and nervous systems came from observations
of the emotional disturbances associated with abnormal
endocrine activity in the thyroid and adrenal medulla.
Graves’ disease (thyrotoxicosis, toxic goiter), for in-
stance, seemed to be triggered by severe psychic distress,
such as a sudden shock or long, continuing anxiety, and
nervous irritability was among its most common symp-
toms. Because clinical manifestations of nervous system
involvement in the thyroid matched anatomical observa-
tions of sympathetic nerves in the thyroid, it seemed
possible that the thyroid’s secretions were directly
controlled by the sympathetic branch of the autonomic
nervous system. Although research in the 1930s con-
centrated instead on the humoral control of the thyroid
by the anterior pituitary’s thyrotropic hormone, the
earlier notions of neural control continued to interest
physicians, psychiatrists, and physiologists (Rolleston
1936, pp. 222-224, 240: Reichlin 1966, pp. 445-446,
502-506).

The isolation and synthesis of epinephrine in the
early years of the twentieth century made it compara-
tively easy to study the relations between the sympa-
thetic nervous system and the adrenal medulla. Almost
immediately after Oliver and Schafer’s discovery of the
pressor effect of adrenal medulla extracts, neurophysiol-
ogists noted how closely the actions of the extract (and
later, of pure epinephrine) mimicked the effects of
the sympathetic nerves. As early as 1904, T. R. Elliot
hypothesized that the sympathetic nerves acted by
releasing epinephrine at the ends of the nerve fibers.
The histology and embryology of the adrenal medulla
hinted at this possibility too, for the medulla was laced
with sympathetic nerve fibers which ended on the
medullary cells, which had themselves developed from
embryonic nerve cells. And, electric stimulation of the
nerves leading to the medulla were found to induce the
medullary cells to secrete epinephrine (Rolleston 1936,
pp. 321-323; Dale 1962, p. 72).

From 1909 on, the American physiologist, Walter
Cannon, emphasized the psychosomatic importance
of the neural connections to the adrenal medulla. In
the course of studying the mechanics of digestion in

cats, he had noticed that whenever sudden noises or
other distractions made the cat angry or afraid, the
movements of its stomach and intestines would stop
equally suddenly. Over the next five years Cannon in-
vestigated the effects of emotional stimuli on epine-
phrine secretion, which led to his famous theory of the
emergency function of the adrenal medulla. In his
1915 monograph, Bodily Changes in Pain, Hunger,
Fear, and Rage, he argued that strong emotions stimu-
lated the sympathetic nerves and thence the secretion
of epinephrine; all the varied effects of the hormone on
the body could be seen as quick preparations for “fight
or flight” (Brooks and Koizumi 1975, p. 52).

Although neural control over the adrenal medulla
and the thyroid seemed probable, the physiological
mechanisms were obscure. How did the nerves provoke
secretion? In 1921 Otto Loewi in Austria showed that
the nerve cells themselves secrete neurohumors, tiny
amounts of chemical substances which travel the short
distance from the secreting end of the neuron to the
membrane of the cell being excited. In one of the most
elegant biological experiments ever devised, Loewi
proved that, when the parasympathetic vagus nerve to
the heart is electrically stimulated, it releases a neuro-
humor which will slow the heart.

H. H. Dale and Loewi subsequently identified this
Vagus-stoff as acetylcholine, a compound which was
already known to mimic the actions of the parasympa-
thetic nerves as closely as epinephrine mimicked the
sympathetic nerves. (Later, acetylcholine proved to be
the neurohumor released by the voluntary nerves as
well.) Meanwhile, Cannon and his co-workers believed
that the sympathetic nerves also liberated chemical
transmitters. After much controversy and reinterpreta-
tion of experimental data and theories, Cannon's young-
er colleague, Bacq, and Ulf von Euler, proved that the
sympathetic nerves do indeed secrete epinephrine
in order to inhibit activity of the target cell, and that
they also release norepinephrine to excite the target
cell (Bacq 1975, pp. 68-76).

The most logical place to look for neuroendocrine
interactions, however, was in the connections between
the brain and the pituitary gland. The posterior lobe
attracted attention first, for anatomically it possesses
a rich supply of nerve fibers which join the lobe to a
tract of the hypothalamus by way of the pituitary
gland’s stalk. Oliver and Schafer’s discovery of internal
secretions from the posterior lobe raised a difficulty,
however: histologically the posterior lobe had many

 
 

nerve fibers but no obvious secretory cells. How then
did it produce its blood-borne effect on blood pressure,
water metabolism, and uterine contraction?

Studies of diabetes insipidus further complicated the
problem. In 1913 two clinical investigators noted the
ability of posterior lobe extracts to relieve the excessive
urine flow of patients with diabetes insipidus. Presum-
ably, in these patients a damaged posterior lobe failed
to secrete enough antidiuretic hormone, but there was
conflicting evidence. Emotional and physiological stress
also seemed to have an antidiuretic effect, which implied
that the nervous system exerted some control over water
metabolism — the parallel to Cannon's emergency theory
of adrenal medulla function was easily drawn (Pickford
1975, pp. 209-210). In 1912 and 1913 Aschner and
Roussy and Camus argued that diabetes insipidus (not
to mention obesity, sexual dysfunction, genital atrophy,
and increased sugar in the blood — many of the symp-
toms, in short, associated with pituitary gland disorders)
were caused by damage to the brain in the hypothalamic
region. In 1920 they produced experimental diabetes
insipidus in dogs by making lesions only in the hypothal-
amus, leaving the pituitary gland untouched, a feat that
led them to deny any function at all to the hypophysis
(Rolleston 1936, pp. 56-56; Abel 1923-24, pp. 202-207;
Harris 1955, pp. 200-204).

These rival explanations of diabetes insipidus and of
the roles of the posterior lobe and the hypothalamus
were gradually reconciled through new studies of the
nerves uniting the brain and hypophysis.® By 1940 it
was reasonably clear that the hypothalamus exerted
direct control over the antidiuretic and oxytocin secre-
tions of the posterior lobe, and that this control was
somehow mediated by the nerves leading from a well-
defined tract of the hypothalamus to the posterior lobe.
The source of the secretions themselves remained a
question that was not fully answered for another decade,
although the most important clues had already been
discovered. Ernst Scharrer had shown in his doctoral
thesis in zoology in 1928 that certain hypothalamic
neurons in fish functioned like glandular secretory
cells, and he and his wife Berta subsequently found
neurosecretory cells in many vertebrate and invertebrate
species. But for many years, in a pattern typical of
resistence to scientific discoveries, they could not
persuade either the endocrinological or the neurological
communities that their cytological evidence would
explain the confusing relationship between the hypothal-
amus and posterior pituitary. For, as Berta Scharrer

65

later wrote, the proposition that there were special
hypothalamic neurons with an endocrine function “‘was
a bold concept that did not fit into any existing mold,
and it is not surprising that it was received with skepti-
cism. Why should members of a class of cells as readily
defined as neurons be capable of functioning as glands
of internal secretion? ”’ As Scharrer goes on to note,
however, ‘What is less understandable. . .is the almost
universal rejection by the scientific community of the
validity of cytological evidence for the existence of a
secretory process’’ (Scharrer 1975 b, pp. 225-260).

After World War 11, an old friend of the Scharrers,
Wolfgang Bargmann, became irritated by the negative
attitude of his fellow scientists toward the Scharrers’
conception of neurosecretion. Bargmann decided to try
a new approach based on the well-known usefulness of
cell staining techniques in endocrinology. His first trial
in 1948-1949 of a recently developed staining technique
succeeded splendidly, for he could see individual neu-
rons of the hypothalamic tract extending themselves
without interruption down into the posterior lobe. By
1957 Bargmann and the Scharrers had established the
fact that the posterior lobe was little more than a
storage depot for the hormones produced by the hypo-
thalamus (Bargmann 1975, pp. 38-43; Scharrer 1975 b).

The connections between the anterior pituitary and
the nervous system were equally hard to understand,
although many observations, especially about the
reproductive functions of the anterior lobe, implied the
existence of connections. For instance, women had
long known that emotional distress and other psycholog-
ical factors can affect their menstrual cycles. Farmers,
hunters, and naturalists had recognized for centuries
that many environmental factors like temperature,
food supply, light, and the sensation of coitus can alter
an animal’s ability to ovulate.

Further evidence came from the clinic: tumors of the
hypothalamus disturbed many endocrine functions
usually associated with the anterior lobe (Fulton,
Ranson, and Frantz 1940, pp. xiii-xxx, 864-874).
Following this lead, Camus and Roussy produced
Frohlich’s syndrome of asexual adiposity by making
minor lesions in certain tracts of the hypothalamus, just
as they had caused diabetes insipidus with lesions in the
tract connected to the posterior lobe. Joseph Hinsey and
Joseph Markee at Stanford brought together in 1933
Markee’s observations on the nervous control of ovula-
tion and Hinsey’s experience with the chemical transmit-
ters of sympathetic and parasympathetic nerves. In a
short note they hypothesized that the lack of direct
nerve fiber connections between the hypothalamus and
the anterior lobe, in contrast to the rich innervation
of the posterior lobe, implied a humoral mechanism for
the brain's control over the anterior lobe’s ovulatory
function (Hinsey 1975, pp. 135, 139). But these various
observations, experiments, and speculations did not
excite much interest until the 1940s. The only mention
of “neuro humoral mechanisms’ in the authoritative
and lengthy 1939 survey, Sex and Internal Secretions,
for example, was to be found in a psychologist’s review
of research on the sex drive (Allen, Danforth, and
Doisy 1939, pp. 1213-1220).

Before anyone could make sense of the miscellaneous
assortment of observed nervous system-anterior lobe
interactions, much more detailed, direct experimenta-
tion on the anatomy and physiology of the hypothal-
amus, pituitary stalk, and anterior lobe was necessary.
It was the English anatomist, G. W. Harris, who ‘more
than anyone else brought the new endocrinology into
focus in the late 1930s’* and 1940s (Price 1975, p. 229).
Although Harris’ early experiments suggested that nerves
led from the hypothalamus to the anterior lobe, his
examination of the lobe’s anatomy raised doubts in his
mind, for the anterior lobe abounded in secretory
cells and blood vessels but almost completely lacked
neurons.

The other possible path for messages between the
central nervous system and the anterior lobe was through
the rich network of blood vessel that surrounded the
pituitary stalk. A Roumanian pathologist, Rainer,
had noticed in 1927 that these blood vessels were
especially prominent in people who had died suddenly
and violently; he persuaded a young medical student,
G. R. Popa, to study these vessels and their connections
to the capillaries of the hypothalamus and the hypo-
physis. Popa and Fielding published an account of this
work in 1930, in which they said that the blood in these
short portal vessels flowed upwards from the hypophysis
to the hypothalamus. Six years later Wislocki and his
colleagues in Boston disputed this assertion and argued
from histology that the blood flowed down from the
brain to the anterior lobe. Wislocki, Popa, and Harris
debated (“at times quite vehemently,” Harris recalled
much later) the question of the direction of blood
flow over the next ten years (Harris 1955, p. 30).

In 1947, Harris and Green tried a new approach:
they now watched the flow of blood directly in living,
anesthetized animals, and in so doing confirmed Wis-

66

locki’s work. The downward flow of blood together
with the absence of direct nerve connections strongly
pointed to the neurohumoral system of control that
had first been proposed in 1933 by Hinsey and Markee.
Harris devoted the next half dozen years to proving
the theory that the hypothalamus sends blood-borne
chemical messengers down the pituitary stalk’s portal
vessels into the anterior lobe, where they stimulate the
release of the anterior lobe’s pituitary hormones (Harris
1955, pp. 20-31; Tepperman 1973, p. 36; Vogt 1972,
pp. 310-313; Jacobson 1975).

Once the neural control over the anterior lobes
secretions were widely accepted, research centered on
isolating the ‘releasing factors.” Early trials with known
nerve transmitter substances showed that these com-
pounds were only indirectly concerned with the hypo-
thalamus/anterior lobe system. In the mid-1950s and the
60s neuroendocrinologists and biochemists succeeded
in assaying, isolating, and purifying a series of small
polypeptides from hypothalamic tissue and blood. By
1973 eleven different releasing or inhibiting factors
had been found, eight of them purified, and the struc-
ture of three worked out in detail (McCann and Dhari-
wal 1966, pp. 261-296; Williams 1974, p. 5; Maugh
1975, p. 921).

As endocrinologists learned to see the anterior
lobe as the ‘‘concert master’ rather than the ‘‘con-
ductor” of the ‘endocrine orchestra,” they recon-
sidered the interactions among the glands that had
been so arduously worked out before. In the 1940s,
Norbert Wiener, the inventor of cybernetics, had pop-
ularized the concept of feedback control in engineer-
ing and in neurophysiology (Dempsey 1975, pp. 85-86;
Wiener 1948, pp. 7-33, 113-114). Walter Cannon's
concept of homeostasis agreed well with Wiener’s ideas,
and endocrinologists gradually realized that the language
of feedback control provided an effective way of de-
scribing and thinking about endocrine interactions. They
saw that the presence of the hypothalamus in the endo-
crine constellation required more elaborate feedback
systems than the simple see-saw reciprocity envisaged
by earlier investigators.

Following the publication of Harris’ monograph,
Neural Control of the Pituitary Gland, in 1955, with its
diagrams of feedback loops involving the higher brain,
the hypothalamus, the two pituitary lobes, the gonads,
adrenals, thyroid, and sympathetic nervous system,
neuroendocrinologists started intensive research into
the mechanisms by which hormones act on the brain

 

 
and hypophysis. The principle of feedback loops has
become so fundamental a part of endocrinological
thinking in recent years that textbooks now commonly
discuss the feedback integration of the endocrine system
before they even name and describe the components
of the system, the glands and hormones (Williams
1974; Tepperman 1968, 1973; Barrington 1975).

Reading the Message: Hormone Receptors
and Molecular Biology

There was a continuity of outlook through the three
phases of endocrine research discussed so far, as re-
searchers concentrated on seeking the source of control
over the actions and interactions of glands and their
secretions. In the earliest phase, control seemed to
come from the gland itself, in the second, from the
hypophysis, and in the third, from the nervous system
as modified by feedback loops. The response of target
organs was used to assay hormones, but otherwise that
response was simply taken for granted. The interactions
of the endocrine system were studied on the tissue or
organ level; and, while biochemists played an important
role in purifying and characterizing hormones, they
could not contribute much to the conceptual founda-
tions of the discipline.

The question, “How do organs and cells receive and
read the hormone message?”’ could not be answered,
or even asked, effectively in this context. It made sense
only at the cellular level, and this was — until the late
1950s — the separate province of molecular biologists
and biochemists. For among biologists ‘‘there was a
widespread feeling. . .that hormone action could not be
studied meaningfully in the absence of organized cell
structure’ (Sutherland 1972, p. 401). Between 1955 and
1962, however, Earl Sutherland and his co-workers,
proceeding on the conviction that ‘there was a real
possibility that hormones might act at the molecular
level,” proved that breaking up cells did not destroy
their sensitivity to some hormones (Sutherland 1972,
p. 401). In studying the influence of epinephrine and
the pancreatic hormone, glucagon, on the liver’s ability
to break glycogen down to glucose, Sutherland and his
associates found in liver cell fragments a molecule called
cyclic AMP which carried the hormone message to the
enzymes that governed the rate of glycogen — glucose
reactions. Since then, cyclic AMP has also been impli-
cated in the cellular reception of information from the
luteinizing hormone, the adrenocorticotropic hormone,
thyroid-stimulating hormone, parathyroid hormone, and

67

 

many others. Its ubiquity in the animal kingdom at
all levels of organization suggests that, in evolutionary
terms, it may be as significant a compound as DNA,
RNA, and ATP (Robison, Butcher, Sutherland 1971,
p. 74 and chap. 12). Research on the biochemical and
structural details of the hormone-membrane receptor-
cyclic AMP-enzyme activation pathways in the cell
has become one of the fastest growing fields in con-
temporary endocrinology and molecular biology.

Sutherland’s discovery of cyclic AMP came directly
out of research on the enzymes and biochemical path-
ways of carbohydrate metabolism — a tradition very
different from endocrinological research in the first
half of this century. Unlike endocrinologists, for ex-
ample, researchers in intermediary metabolism had
long been accustomed to experimenting with cell-
fragments and with enzyme-substrate reactions in cell-
free systems. Another difference lay in the primary
research orientation of investigators such as Sutherland.
His mentors Carl and Gerty Cori, and others who eluci-
dated metabolic pathways in the 1920s, 30s, and 40s,
had medical training and clinical experience, and their
work was supported largely by medical schools and
medical research institutes. But they conducted their
research on the hormonal control of carbohydrate
metabolism in the tradition of basic research, with
questions about the cause or cure of disease playing
little part in their discoveries (Sutherland 1972, pp.
401-408; Cori 1969, pp. 1-20).

Virtually all areas and phases of endocrinology,
however, are marked by recurring interactions between
basic and clinical pursuits, and contemporary molecular
endocrinology is no exception. Thus, cyclic AMP work-
ers have begun looking into the relationship between
defects in the formation or action of this nucleotide and
a variety of human diseases, with the ultimate hope that
“The results of this research can eventually be applied
to increase the quality of human life. . .[since] the chief
end of all scientific research either is or ought to be
the promotion of human happiness’’ (Robison, Butcher,
and Sutherland 1971, pp. 454-455). Simultaneously,
the reverse application of knowledge from the study of
disease to fundamental questions — so common in the
earlier history of endocrinology — is also taking place
in the new molecular endocrinology. For example,
physicians have known for some time that the lethal
effect of the cholera bacteria’s enterotoxin is a devas-
tating diarrheal loss of fluids and salts from the body;
the most effective therapy is the immediate replacement

 
 

of the lost fluids and salts. Recent research on the
mechanism of the toxins action has shown that the
toxin mimics the ability of cyclic AMP in intestinal
cells to provoke cell membranes into actively transport-
ing fluid and salts out of the cells. Carpenter theorizes
that the toxin behaves like a hormone by binding itself
to hormone receptors on the cell membrane; the recep-
tors stimulate production of cyclic AMP, which in turn
stimulates the membranes active transport system.
Unlike ordinary hormones, though, cholera enterotoxin
is not particular about the kinds of cells or the mem-
brane binding sites it will act upon. This makes it a use-
ful, if potentially fearsome tool for investigating basic
questions about the structure of hormone receptors
and about the biochemical role of cyclic AMP within
the cell (Carpenter 1972; McCann 1974, pp. 323-325).
Thus, the discovery and study of diseases stemming from
cyclic AMP malfunction promises to yield both the
objective of treating diseases more effectively, and also
that intense intellectual satisfaction which comes to the
scientist when his puzzle-solving researches fit together
to produce a new understanding of life processes.

“A New Physiology”

As we have explored some of the ways in which
endocrinology has evolved from ancient ‘kitchen
anatomy’ to present molecular researches, we see
clearly the interplay between the clinic and the research
laboratory in the generation of problems, concepts, and
facts concerning endocrine function. What we have
called phases three and four of endocrine research — the
development of neuroendocrinology and current molec-
ular studies of hormone action — belong primarily to
that portion of endocrinology’s history where research
had moved from a disease-initiated focus into the prov-
ince of basic research. We have, accordingly, treated
these phases only briefly, to suggest where that flow
led and is leading investigators of the ductless glands.

It is in looking at the emergence of endocrinology
as a field of biology in the latter decades of the nine-
teenth century and early years of the twentieth century
that we see, most preeminently, the imprint and influ-
ences of medical concerns. For, particularly in France
and then Britain, countries in which clinical medicine
more generally shaped the problems pursued by physiol-
ogists, attention by physicians to disorders of the duct-
less glands provided a new range of phenomena for
scientific investigation. At the turn of the century, as
represented most significantly by Bayliss and Starling’s

researches, clinical work united with advances in chem-
istry, bioassay methods, and physiology to generate a
new and fundamental understanding of the role of the
endocrine gland’s chemical mediators in physiological
and biochemical functioning.

Reflecting in 1933 on the impact of endocrinology
upon not only medicine but upon physiology as well,
R. G. Hoskins chose to underscore the words of the
great British physiologist and pioneer endocrinologist,
Edward Sharpey-Schafer:

The changes in physiology which have resulted
from this [new endocrine] knowledge constitute
not merely an advance in degree but an alteration
in character. The doctrine of internal secretions
forms a new departure. We must in the future
explain physiological changes in terms of chemical
regulation as well as of nervous regulation. It is
therefore justifiable to speak of the doctrine as
a New Physiology, seeing that it has completely
altered our outlook on many of the problems with
which physiology deals and consequently on those
met with in medicine and surgery. (Hoskins 1933,
pp. 347-348)

 
1. Within the confines of a single chapter, we have had to
omit some of the most interesting fundamental consequences
of disease-related research in endocrinology. Some examples
drawn from the history of diabetes and insulin research will
give some sense of the range of problems suggested by clinical
endocrinology and some sense of our omissions.

Clinical endocrinologists have imposed great demands on the
ingenuity of biochemists, to the benefit of both. For example,
the first protein to have its amino acid sequence worked out
completely was insulin. Sanger demonstrated conclusively by
his analysis of the hormone that ‘proteins are well-defined
molecules in which the amino acid units are linked by peptide
bonds to form long polypeptide chains,” a definition that was by
no means certain when he began his decade of work in 1945.
In the process of analyzing the structure of the insulin molecule,
Sanger developed an armory of biochemical techniques for
attacking the structure of other proteins and macromolecules.
These techniques soon revealed subtle differences among the
insulins of different species and forced evolutionary biologists
to ask why, for example, pig insulin resembles human insulin
more than cow insulin does.

Through both human and animal research on the nature of
endocrine disorders, investigators have discovered both how
universal endocrine mechanisms are in the animal kingdom and
how idiosyncratic each group can be. A 1972 review of research
on diabetes, insulin, and carbohydrate metabolism, for example,
points out that insulin is an especially important hormone in
carnivores who cannot count on a steady supply of food and
whose metabolism must cope with sudden gluts and long-term
shortages. In such creatures — man included — diabetes will be
a serious disease; in herbivores and especially the ruminants
who nibble all day long, diabetes is much less dangerous (Fritz
1972, pp. 166-180).

Another area we do not treat is that of comparative endo-
crinology. We deal only with research on the endocrinology of
vertebrates; and within the vertebrates, almost solely with
laboratory animals — dogs, cats, rats, rabbits — and man. We
bypass entirely the fascinating work on invertebrates, plants,
fungi, algae, and bacteria. Moreover, we have ignored the contri-
butions of clinical endocrinology to our understanding of
evolution, ecology, social and sexual behavior, psychology,
embryology, and development. Finally, we have played favorites
within the endocrine system too. Thus, for example, the story
of parathyroid and calcium metabolism receives no mention.
The elaborate relationships of the sex hormones and glands
with reproduction, growth, development, and behavior are only
touched upon, chiefly because the history of sex endocrinology
currently is being dealt with extensively by historian Diana
Long Hall.

2. The importance of special instruments for the advance-
ment of both neuroendocrinology and neurosurgery is illustrated
by the stereotaxic instrument developed in 1908 by British
neurosurgeon and neurophysiologist Victor Horsley and his
colleague R. H. Clarke. The Horsley-Clarke device, a special kind
of head-clamp combined with three-dimensional micrometer

Notes

69

 

measuring devices, enabled physicians and laboratory researchers
to make surgical or electrolytic lesions in precisely determined
spots in the brain.

3. For instance, the discovery was the basis for Dorothy L.
Sayer’s 1928 short story, ‘The Incredible Elopement of Lord
Peter Wimsey."’

4. The diuretic response later was shown to be an artifact
due to the experimental conditions, in contrast to the antidiure-
tic response which is an endocrine function of the posterior
pituitary (Barrington 1975, p. 93).

5. Despite their obvious importance, these discoveries of
the growth hormone and the diabetogenic effect of the anterior
pituitary were something of a side issue for Evans and his col-
leagues. So was the laboratory group's participation in the dis-
covery of the thyroid-stimulating hormone (TSH) and the
adrenocorticotropic hormone (ACTH), both hinted at in Evan's
analysis of Smith's early research on tadpoles (Evans 1923-24,
pp. 216-218; Evans, Sparks, and Dixon 1966, pp. 319-320;
Amoroso and Corner 1972, pp. 129-131). The interrelationships
between the hypophysis and the ovaries remained the central
problem for Evans and his co-workers. In seeking the reasons
why their gigantic rats who had been treated with growth
hormone failed to ovulate, Evans, Simpson, and Smith uncov-
ered the existenc@ of still another pair of hormones, the gonado-
tropic luteinizing hormone (LH) and follicle-stimulating hor-
mone (FSH). Their method of preparing crude extracts of
growth hormone had, they gradually realized, retained both the
growth hormone and the luteinizing hormone but destroyed
the follicle-stimulating hormone. For successful ovulation both
gonadotropic hormones had to be present in the right propor-
tions. Once distinctions among the effects of the luteinizing,
follicle-stimulating and growth hormones were drawn and
analogous effects of these hormones in male animals were recog-
nized, the research effort turned to the isolation and purification
of the three hormones; in 1949, Li, Simpson, and Evans finally
obtained homogenous FSH.

6. In the 1930s at Chicago, Fisher, Ingram, and Ranson used
the Horsley-Clarke stereotaxic instrument to make small, accu-
rately placed lesions in different areas of the hypothalamus in
cats (see note 2). Lesions in the tract originally described by
Ramon y Cajal had two related effects: atrophy of the posterior
pituitary, and a polyuria very much like that in clinical cases
of diabetes insipidus. Ranson and his colleagues also noticed that
these lesions interfered drastically with labor in pregnant cats —
a result which correlated well with the strong uterine contrac-
tions invoked by the oxytocin (‘quick childbirth’’) fraction of
posterior lobe extracts. Injections of posterior pituitary extract
counteracted the polyuria and difficult labor. Lesions in other
tracts of the hypothalamus did not incur any of these disorders
although they did have other effects resembling pituitary mal-
function (Harris 1955, pp. 200-204, 224-225).

 
 

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CHAPTER 5
“THE LESSON OF RARE MALADIES”

 

SICKLED CELLS, MOLECULAR DISEASE, AND THE GENETIC CONTROL
OF PROTEIN STRUCTURE

Much of our present understanding of the composi-
tion, structure, and function of genes has come from the
joining of previously disparate work in microbiology,
biochemistry, and genetics, a fusion that marked the
emergence of molecular biology in the 1940s.! Since
the 1940s, investigators seeking to elucidate gene func-
tion have turned by-and-large from the morphological
and biochemical complexities of the fruit fly, mice,
and maize, materials they had used to unravel problems
of gene transmission, to simpler microbial and viral
materials. To contemporary geneticists and molecular
biologists, aware of the infinitely greater complexities
of the human organism, it thus seems ‘remarkable’
and ‘amazing’ that, stemming from work on a human
hereditary disorder, sickle cell anemia, ‘‘the genetically
controlled protein system about which most is known
is human hemoglobin’ (Sutton 1961, p. 50).

In this chapter we will see how ‘‘the existence of
mutant proteins in humans afflicted with sickle cell
anemia proved to be the critical key in the elucidation
of the nature of the genetic apparatus’’ (Handler 1970,
p. 664). As in our other case studies, it is a story in
which a clinical problem feeds into and affects the
course of a stream of biological research, a stream
which is fed by many sources and which in turn has
numerous branches. It also is a story that relates how
much we have learned from what the British physician,
Sir Archibald Garrod, called ‘“‘the lesson of rare mala-
dies,”” the inherited abnormalities that provide research-
ers with a “natural experiment.”’ In this case, the natural
experiment, sickle cell anemia, led to the concept of
“molecular disease’’ and thence to a frontal assault
on the question of how genes control protein structure.
And, in delineating how gene mutations alter the struc-
ture of the human hemoglobin molecule, researchers
have made major strides in resolving one of the oldest
and most difficult problems in genetics, the problem
of allelism. (Alleles are alternative or variant forms of
genes which occur at the same locus or place on two
members of a pair of homologous chromosomes.) “The
problem of allelism,”” as Levitan and Montagu explain,

73

“arises whenever two traits are found that affect the
same cell, tissue, or organ system. . .[For example]
every time a new red blood cell antigen, or blood type is
discovered, the question arises as to whether it repre-
sents a further complexity of a known system (and thus
probably conditioned by a new allele at a previously
discovered locus) or whether it is a new system condi-
tioned by still another independent locus. This problem
goes to the very core of genetics. We are in effect look-
ing for evidence to delineate the unit factor of genetics,
the gene’’ (Levitan and Montagu 1971, p. 549).

Inborn Errors of Metabolism: Garrod’s
Unlearned Lesson

Conceptually, the bearing of sickle cell research on
our understanding of the function of genes is indirectly
but inextricably linked with the ideas of Sir Archibald
Garrod (1857-1910) concerning the biochemical nature
of gene action. Garrod, who died the same year that the
first clinical report of sickle cell anemia was published,
worked in that post-Mendelian era when genetics and
biochemistry were pursued largely as separate endeavors.
When those fields were joined, his clinically-based con-
cept of inborn errors of metabolism would be redisco-
vered and reenunciated as the one gene-one enzyme
concept, on the basis of research with the bread mold,
Neurospora. Then, in the 1950's, once again growing
out of a clinical framework, this time provided by sickle
cell anemia, Garrod’s ideas would find their modern
echo in the one gene-one polypeptide concept of the
genetic control of protein structure.

In 1902 Garrod, an Oxford-trained pathologist,
published the first of a series of papers on alkaptonuria,
a disorder manifested clinically by a blackening of the
urine on exposure to air. Six years later, in the Royal
Society's Croonian Lectures, Garrod summarized his
first decade of researches on alkaptonuria and three
other human disorders, albinism, cystinuria, and pento-
suria, four “rare maladies’’ that he termed ‘inborn
errors of metabolism.” In his lectures, published in 1909
with a second edition in 1923, Garrod “clearly and

 
 

 

explicitly interpreted [alkaptonuria]l and the other
‘inborn errors of metabolism’ as blocks at specific points
in the normal pattern of intermediary metabolism,
where some specific enzyme, normally present, was
absent because of alteration of the controlling gene’
(Glass 1965, p. 231).

Garrod, a physician thoroughly trained in the biolog-
ical and chemical sciences of his time, drew upon and
uniquely joined contemporary researches in protein
biochemistry and in the newly rediscovered science of
Mendelian genetics. As he pointed out in the first of
his 1908 Croonian lectures:

The great strides which recent years have wit-
nessed in the sciences of chemical physiology and
pathology, the newly-acquired knowledge of the
constitution of proteins and of the part played by
enzymes in connexion with the chemical changes
brought about within the organism, have pro-
foundly modified our conceptions of the nature
of the metabolic processes. . .The conception of
metabolism in block is giving place to that of
metabolism in compartments. The view is daily
gaining ground that each successive step in the
building up and breaking down, not merely of
proteins, carbohydrates, and fats in general, but
even of individual fractions of proteins and of
individual sugars, is the work of special enzymes
set apart for each particular purpose. (Garrod
1909, pp. 4-6)

In introducing his audience to the anomalies ‘‘which
may be classed together as inborn errors of metabolism,”
Garrod first distinguished them from ‘‘diseases of
metabolism’ such as diabetes, gout, and obesity. “The
liability to develop diabetes or gout is often inherited,
but the diseases themselves are not inherited for they
are never congenital. Developing at any period of life,
the mischief, once begun, tends to become aggravated
as time goes on, but the rate of aggravation differs
widely in individual cases and is often conspicuously
controlled by appropriate treatment’ (Garrod 1909,
p. 131). In contrast to these diseases, Garrod explained,
some of the inborn errors of metabolism ‘‘are certainly,
and all of them are probably, present from birth.”
Clinically, he stated,

The chemical error pursues an even course and
shows no tendency to become aggravated as
time goes on. With one exception they bring

74

in their train no serious morbid effects, do not
call for treatment, and are little likely to be
influenced by any therapeutic measures at our
disposal. Yet they are characterized by wide
departures from the normal of the species far
more conspicuous than any ordinary individual
variations, and one is tempted to regard them as

metabolic sports, the chemical analogues of
structural malformations. (Garrod 1909, pp.
13-14)

Today's thick textbooks devoted to inborn errors of
metabolism bear witness to Garrod’s insight in 1908
that “among the complex metabolic processes of which
the human body is the seat there is room for an almost
countless variety of such [metabolic] sports.” But he
acknowledged that in his own day there was adequate
evidence for classifying only four anomalies as inborn
errors of metabolism.

Of the four, alkaptonuria was Garrod’s most compre-
hensively analyzed inborn error of metabolism. For a
substantial body of clinical, biochemical, and hereditary
information about alkaptonuria existed by 1908, includ-
ing Garrod’s own investigations, which he uniquely
synthesized and interpreted. The blackened urine of
alkaptonuria was known to be caused by the excretion
of homogentisic or “‘alkapton’’ acid, a substance formed
in the body from tyrosine and phenylalanine. Garrod
recognized that “‘two explanations are possible of the
fact that alkaptonurics excrete homogentisic acid,
whereas normal persons do not. Either the alkapton
acid is a strictly abnormal product formed by a per-
verted metabolism of tyrosin and phenyl-alanine. . .or
it is an intermediate product of normal metabolism
which is usually completely destroyed and does not
come to excretion, but which in alkaptonuria escapes
destruction’ (Garrod 1909, p. 66). Garrod then docu-
mented his reasons for concluding that the second of
these hypotheses was the correct one. Homogentisic
acid, he argued, is a product of normal metabolism, but
the alkaptonuric, unlike the normal individual, lacks
the “power of destroying homogentisic acid when
formed - in other words of breaking up the benzene
ring of that compound” (Garrod 1909, p. 79). This
inability, Garrod correctly speculated, was due to the
absence or inactivity of an enzyme that normally cata-
lyzes the breakdown of homogentisic acid.? “We may
further conceive,” he wrote, ‘that the splitting of the
benzene ring in normal metabolism is the work of
a special enzyme, that in congenital alkaptonuria this
enzyme is wanting, whilst in disease its working may
be partially or even completely inhibited” (Garrod
1909, p. 80).

Garrod’s recognition that the metabolic defect in
alkaptonuria represented an inborn or inherited condi-
tion, in turn, was based on familial patterns of the
disease’s occurrence. From familial studies, Garrod
found that the four metabolic disorders he was analyzing
had ‘‘the liability for each of them to occur in several
members of a family, most often in collaterals of the
same generation, born of normal parents’ Garrod 1909,
p. 22). An explanation for the inborn error’s mode of
inheritance within such families was provided by William
Bateson, who was responsible for having Mendel’s
paper translated into English, was the first to demon-
strate Mendelian inheritance in animals, and who intro-
duced such terms as ‘‘genetics’’ and ’‘allelomorph.”’
Drawing upon Bateson’s 1902 report to the Evolution
Committee of the Royal Society on “The Facts of
Heredity in The Light of Mendel’s Discovery,” Garrod
concluded that ‘““the mode of incidence of alkaptonuria
finds a ready explanation if the anomaly in question be
regarded as a rare recessive character in the Mendelian
sense’’ (Garrod 1909, p. 26). In /nborn Errors, he
examined at length the Mendelian nature of alkaptonuria
as a recessive trait, and also presented evidence for
pentosuria, cystinuria, and albinism as metabolic defects
due to the recessively inherited absence of a single
enzyme. “To the students of heredity,” Garrod pointed
out a scant eight years after the rediscovery of Mendel's
work, ‘the inborn errors of metabolism offer a promis-
ing field of investigation.” However, he wisely cautioned
those who would enter the arena of medical genetics,
“their adequate study from this [genetic] point of view
is beset with many difficulties” (Garrod 1909, p. 22).

One Gene-One Enzyme. The Rediscovery
of Garrod’s Concept

When Garrod delivered his Croonian Lectures in
1908, the prevailing concept of gene action offered by
the nascent science of genetics was ‘one gene-one char-
acter.” As Bentley Glass observes, Garrod’s pioneering
foray into biochemical genetics represented two major
steps forward from this early understanding of gene
action: “from recognition of the relation of the specific
altered gene to the particular blocked step in the meta-
bolic pattern, and thence to the lack of the specific
enzyme governing that pattern’’ (Glass 1965, p. 233).

75

 

But Garrod might well have echoed Gregor Mendel’s
bitter words, “Meine Zeit wird schon kommen’ [my
time will surely come], for the import of the British
physician's work, like that of the Austrian monk's,
would be unrecognized by geneticists, and by bioche-
mists, for several decades.

For those interested in understanding the processes
of biomedical discovery, innovation, and diffusion, the
question of why work such as Garrod’s was ‘‘profoundly
neglected’’ during his lifetime is as interesting and signi-
ficant as the content of the work itself. As with other
instances of scientific and clinical discoveries that under-
went a long latency period before they were ‘‘redisco-
vered,”” there are multiple explanations of why Garrod’s
biochemical-genetic concept of gene action lay fallow
for many years. One partial explanation, advanced by
Garrod’s principal rediscoverer, George Beadle, invokes
the familiar argument that ‘‘the time was not ripe.”
Because Garrod was ahead of his time, Beadle argued,
neither biochemists nor geneticists would take his con-
cept seriously. Further, Beadle wrote, “I strongly sus-
pect that an important common component of the
unfavorable climate for receptiveness in these two
instances [Mendel and Garrod] is the persistent feeling
that any simple concept in biology must be wrong”
(Beadle 1966, p. 31).

Other, interrelated explanations have been presented
by geneticist and historian Bentley Glass, who also
has studied the reception of Mendel’s work. Glass argues
that Garrod’s lectures on human heredity must have
been known to geneticists, as was Mendel’s 1865 paper
in its time. But Garrod, a physician, was presenting
studies in biochemical genetics in an era when genetics
and biochemistry were separate fields of inquiry. As
late as 1946, Beadle still felt the need to urge the fusion
that Garrod had personified.

If the maximum possible understanding of what
the organism is and what it does is to be obtained,
it is clear that our approach must be made from
many sides. . .the chemist cannot understand what
the organism does chemically without considering
genes. Therefore, the methods of genetics, which
are biological — not chemical, must supplement
those of chemistry. In the same way, a biologist
would be blind if he were to ignore chemistry in
his attempts to understand how the organism is
built and how it functions. Biochemical genetics
represents an approach in which the cooperation
of two disciplines is essential. (Beadle 1946, p. 53)

 
 

Further, as Garrod recognized, research into clinical
inborn metabolic disorders presented many problems
for the geneticist. Thus, ‘there was a common attitude
among geneticists who worked with Drosophila or
maize or other experimental organisms that human
heredity was refractory to analysis and that little basic
insight could be gained from studies of hereditary
abnormalities in an organism that could not be bred at
will” (Glass 1965, p. 232).

Compounding the problems of receptivity created
by a physician working in human biochemical genetics,
Glass continues, was the relative lack of direct interest
in enzymes among geneticists. There were relevant lines
of research pursued by a small group of geneticists,
particularly on the topics of flower pigmentation and
the fermentation of sugars by yeasts, and by 1940 these
researches had ‘‘established that many biochemical
reactions are, in fact, controlled in specific ways by
genes’’ (Beadle and Tatum 1941, p. 499). But how this
genetic control is exerted was unclear, and there was
debate as to whether enzymes were genes themselves
or merely products of genes. An answer had been
proffered by Garrod in 1908, but most of those working
through the early 1940s were either unaware of /nborn
Errors or, if they had read it, failed to see the signifi-
cance of Garrod’s concept.?

For multiple reasons, then, it was not until the mid-
1940's that Garrod’s concept of gene action - one
gene/one metabolic block/one enzyme deficiency
would be “rediscovered’”” and clearly enunciated as
the one gene-one enzyme hypothesis. The name linked
most closely with this rediscovery is George W. Beadle,
who in the 1930s and 1940s conducted Nobel Prize
winning researches cn how genes act on development.
Beadle’s first researches, conducted with Boris Ephrussi,
were carried out on eye pigments of Drosophila. The
hypothesis that he and Ephrussi formulated to explain
their initially unexpected experimental results, Beadle
later reflected, “was a scheme closely similar to that
proposed by Garrod for alkaptonuria. . .But at the
time we were oblivious of Garrod's work, partly because
geneticists were not in the habit of referring to it,
and partly through failure of ourselves to explore the
literature. Garrod’s book was available in many libraries’’
(Beadle 1958, p. 592).

In 1937, Beadle, now working at Stanford, was joined
by a young biochemist, Edward L. Tatum. They found
that “isolating the eye-pigment precursors of Drosophila
was a slow and discouraging job,”” and ‘realized this was
likely to be so in most cases of attempting to identify
the chemical disturbances underlying inherited abnor-

76

malities; it would be no more than good fortune if any
particular example chosen for investigation should prove
to be simple chemically’ (Beadle 1958, p. 594).

Thus, Beadle and Tatum realized, the biochemical
study of gene function required a new approach and
new biological material, something less morphologically
complex than the fruit fly or other diploid organisms
that had been suitable for defining the laws of genetic
transmission. The new approach they selected, Beadle
feels, was an ‘‘obvious one,” but at the time it repre-
sented a “bold step” of “inverting the experimental
attack on the problem [of gene action]. Instead of
waiting for the accumulation of information necessary
to understand the biochemical basis of the complex
morphological mutants of the higher forms, attention
was turned to simpler microbial material” (Handler
1970, p. 25).*

The organism chosen by Beadle and Tatum was the
now famous bread mold, Neurospora crassa (see Beadle
1964; Tatum 1964; and Beadle and Tatum 1941). “It
is sometimes thought,” Beadle said in his 1958 Nobel
Prize address, ‘‘that the Neurospora work was responsi-
ble for the ‘one gene-one enzyme’ hypothesis - the
concept that genes in general have single primary func-
tions, aside from serving an essential role in their own
replication, and that in many cases this function is to
direct specificities of enzymatically active proteins.
The fact is that it was the other way around - the hy-
pothesis was clearly responsible for the new approach”
(Beadle 1958, pp. 596-597). For, as Beadle and others
understood in retrospect, the one gene-one enzyme
concept had been gradually albeit implicitly envolving
in the work of many investigators since it was formu-
lated by Garrod in 1908. Once he was aware of Garrod's
work, Beadle realized that:

In this long and roundabout way, first in Droso-
phila and then in Neurospora, we had rediscovered
what Gerrod had seen so clearly so many years
before. By now we knew of his work and we were
aware that we had added little if anything new in
principle. We were working with a more favorable
organism and were able to produce, almost at will,
inborn errors of metabolism for almost any chemi-
cal reaction whose product we could supply
through the medium. Thus we were able to demon-
strate that what Garrod had shown for a few genes
and a few chemical reactions in man, was true for
many genes and many reactions in Neurospora.
(Beadle 1958, p. 526)

 
The Discovery of Sickled Cells

At the time, no one could have foreseen the connec-
tion between Garrod’s work, or the later researches of
Beadle and Tatum, and the publication of a paper by
Chicago physician James B. Herrick on “Peculiar and
elongated sickle-shaped red blood corpuscles in a case
of severe anemia.” ‘This case is reported because of the
unusual blood findings, no duplicate of which | have
ever seen described,” Herrick wrote in 1910. He had
first seen his patient, a 20 year old black who had been
raised in the West Indies, when he came to Herrick’s
hospital in 1904 with a cough, fever, weakness, diz-
ziness, a headache and nasal discharge, a yellow tinge to
the whites of his eyes, and a history of skin ulcera-
tions. The physician's examination revealed one striking
finding: a large number of red blood cells which, in
contrast to normal red cells, had a nucleus and were
oddly shaped.

Nucleated reds were numerous, 74 being seen in
a count of 200 leukocytes, there being about
5,000 to the c.mm. The shape of the reds was
very irregular, but what especially attracted atten-
tion was the large number of thin, elongated,
sickle-shaped and crescent-shaped forms. . .They
were not seen in specimens of blood taken at the
same time from other individuals and prepared
under exactly similar conditions. They were
surely not artifacts, nor were they any form of
parasite. . .in the fresh specimen where there was
a slight current in the blood before it had become
entirely quiet, all of the red corpuscles, the elon-
gated forms as well as those of ordinary forms,
seemed to be unusually pliable and flexible, bend-
ing and twisting in a remarkable manner as they
bumped against each other or crowded through
a narrow space and seeming almost rubber-like
in their elastic resumption of the former shape.
One received the impression that the flattened
red discs might by reason of unusual pliability be
rolled up as it were into a long narrow bundle.
Once or twice | saw a corpuscle of ordinary form
turn in such a way as to be seen on edge, when its
appearance was suggestive of these peculiar forms.
(Herrick 1910, pp. 518-519)

After a month of treatment (rest, nourishment, and
iron for his anemia) the patient was discharged. His
condition was improved but the odd-shaped and nucle-

77

 

ated red cells were still present. Herrick kept track of
the patient until early 1907, recording his hospitaliza-
tions for problems such as ‘muscular rheumatism’’ and
“bilious attacks.” Clinically, Herrick acknowledged,
“no conclusion can be drawn from this case.” He and
a colleague had unsuccessfully attempted to reproduce
the types of red cells seen in the patient, which sug-
gested to Herrick ‘‘that some unrecognized change in
the composition of the corpuscle itself may be the
determining factor.” However, Herrick concluded, “the
question of diagnosis must remain an open one unless
reports of other similar cases with the same peculiar
blood-picture shall clear up this feature’ (Herrick 1910,
p.521).

Other reports were forthcoming, which confirmed
and elaborated upon Herrick’s clinical findings and
began to explore the possible etiology of the newly
recognized disorder. A second puzzling case of severe
anemia with sickle-shaped cells was reported in 1911 by
Washburn, and a third in 1915 by two physicians from
Washington University Medical School in St. Louis.
“It will be seen that there is a striking similarity in
both the blood-picture and the clinical history of our
case with those of Herrick and Washburn,” wrote Drs.
Jerome Cook and Jerome Meyer. The three patients
“were of Negro blood’ and had “peculiar. . .recurring
leg ulcer,” severe anemia, and a “peculiar discoloration
of the sclerae’’ (the coating of the eyeball). “A glance
at the blood slides leaves no doubt as to the identical
character of the elongated and sickle-shaped red cells”
(Cook and Meyer 1915, pp. 650, 651).

As had Herrick and Washburn, Cook and Meyer
ruled out syphilis or a parasitic infection as causative
agents of the strange disorder. They were able to suggest
another possible explanation for the disease, however,
based on investigations they had conducted with Dr.
Victor Emmel, a colleague ‘who has made extensive
studies of blood development and morphology.”

The possibility of an inherited anomaly suggested
itself. The fact that the three other children of the
family had suffered from severe anemia encour-
aged investigation in this direction. Examination
of the father’s blood showed 4,500,000 red cells,
11,100 white cells, and 86 per cent hemoglobin. . .
the stained smear showed none of the peculiarities
of the daughter's blood. Dr. Emmel, however,
found some resemblance in the behavior of the
blood. When preparations of the fresh blood were

 
 

sealed under precautions which insured sterility
and allowed to stand for several days at room
temperature, the microscope revealed long, sharp
projections and elongations from many of the red
cells in the blood of both the father and the
daughter. Dr. Emmel has not found similar appear-
ances in the blood of any other person. (Cook and
Meyer 1915, p. 649)

In his observations of the father’s blood, Emmel had
seen the phenomenon of sickling in the otherwise nor-
mal-looking red blood cells of carriers, a phenomenon
that the physicians correctly interpreted as suggesting a
hereditary disorder. Emmel’s primary interest in this
case was to explain the sickling process, and in a 1917
paper he reported in more detail on his studies of blood
samples from Cook and Meyer's patient and her father.
Based on these studies, and his knowledge of the deve-
lopment of the blood cells, he proposed a logically
consistent hypothesis about the mechanism of red cell
sickling. Knowing that undeveloped red blood cells
within the bone marrow are spherical in shape, Emmel
proposed that sickling is “‘in part due to an accentuated
or abnormal activity of the same factor which in normal
hematogenesis are involved in the transformation of the
original spherical erythrocyte [red blood cell] into a
biconcave disc-shaped form’ (Emmel 1917, p. 598).

While Emmel’s hypothesis would be proved incorrect,
it directed other investigators toward a fruitful line of
research into the nature of the sickling process. In a
major paper of 1927, E. V. Hahn and E. B. Gillispie
reviewed the growing body of clinical literature on
“sickle cell anemia” - a term introduced by Mason in
1922 - and reported on their own experimental study
of sickle cell formation. Hahn and Gillispie set up a gas
chamber apparatus under the microscope, along with
red blood cell preparations from a patient with sickle
cell anemia, and treated the cells with different gases.
When oxygen or carbon monoxide was added to the
preparation, the sickle cells immediately returned to the
normal discoid shape. When carbon dioxide was added,
it took only four minutes for all the normal discoid
cells to sickle. In addition to this experiment, they also
observed the red blood cells at various partial pressures
of oxygen, and found that the normally shaped cells
of a person with sickle cell trait sickled when oxygen
tension fell below 45 millimeters, less than a third of
normal oxygen.

The gas chamber experiment simulated different
conditions of hemoglobin, the substance in red blood

78

cells that in an oxygenated state combines with oxygen
and transports it throughout the body, and in a deoxy-
genated state acts to remove carbon dioxide. Based on
their study, Hahn and Gillispie were the first to suggest
the role of hemoglobin in sickle cell anemia, which they
too viewed as a hereditary disorder.

The red corpuscles of persons with the “‘sickle cell
trait’ are transformed into sickle cells in vitro as
a result of asphyxia. The transformation takes
place when the oxygen tension falls below a partial
pressure of 45 mm. of mercury. Oxygen and car-
bon monoxide induce restoration of the discoid
form.

All of the facts relating to sickle cells are consis-
tent with a hypothesis that the sickle form is
stable when the hemoglobin is dissociated, and
that the discoid form is stable when the hemo-
globin is combined. . .

Reasons exist for believing that the only specific
cause for active sickle cell anemia is the unique
hereditary anomaly of the red corpuscles which
predisposes to it. (Hahn and Gillispie 1927,
p. 254)°

While Cook, Meyer, and Emmel had proposed in
1915 that sickle cell anemia was hereditary, it would
be more than 30 years before the correct mode of
inheritance was worked out. In the interim, investigators
often grouped together persons with sickle cell anemia
and those who were only carriers of the disease, and the
literature presented an understandably confusing array
of terminology. Thus, for example, Hahn and Gillispie
attempted to replace the ‘“‘awkward’’ terms “‘sickle cell,”
“latent sickle cell anemia’ (clinically healthy but with
the inherited trait) and “‘active sickle cell anemia,” with
terms derived from the Greek word for “‘sickle’’: ““dre-
panocyte,’”” ‘‘drepanocytemia,” and ‘“‘drepanocytic-ane-
mia’’ (Hahn and Gillispie 1927, p. 254).

A first attempt to explain the inheritance of sickle
cell anemia in Mendelian terms was made in 1923 by
J. G. Huck and W. H. Taliaferro. Based on their study
of two families, and in the absence of differentiation
between the trait and the disease, Huck and Taliaferro
concluded that “‘sickle cell anemia in man is an inherited
condition and behaves as a single Mendelian character
which is dominant over the normal condition and which
is not sex-linked’’ (Taliaferro and Huck 1923, p. 597;
see also Huck 1923).

 
Taliaferro and Huck’s explanation of sickle cell
anemia as due to the inheritance of a single dominant
“character’’ or gene was widely accepted until the late
1940's, when it was disproven in the light of a more
sophisticated understanding of homozygous and hetero-
zygous modes of inheritance.’ In the interim, research-
ers also sought to resolve the confusion between sickle
cell anemia and sickle cell trait and to determine whether
the trait and the disease were limited to the black
population. A trio of investigators from University of
Tennessee's Department of Clinical Pathology and the
Nutritional Division of the University of Florida's
Experimental Station clarified many of these questions
about sickled cells through their survey of ‘‘normal
and hospital negroes and white people’’ in the early
1930s. Based on their studies of over 8,000 individuals,
and on other surveys reported in the literature, Diggs,
Ahmann, and Bibb found that the incidence of the
sickle cell trait among negroes was 7.3 percent, and that
1 in 40 of those with the trait also would exhibit sickle
cell anemia. “The sickle cell trait,’ they reported,
“has not been demonstrated in recorded surveys of
white people, and the only reasonably proved instances
of the sickle cell trait in families with unmixed blood
have been limited to those of the Mediterranean stock’
(Diggs et al. 1933, p. 777). Those exhibiting the sickle
cell trait without severe anemia, Diggs and his colleagues
emphasized, should not be considered as ill, for their
observation showed that ‘‘the trait is compatible with
long life” and ‘‘the incidence [of the trait] in hospital
cases has not been proved to be higher than in healthy
individuals.” Thus, they concluded, ‘‘the importance
of the sickle cell trait appears to be limited to the
relatively small group who in addition to the trait
have sickle cell anemia’ (Diggs et al. 1933, p. 777).
But why some of those who inherit the trait, “thought
to be transmitted as a dominant Mendelian character-
istic,” also develop severe anemia remained a mystery -
“due to factors unknown’ (Diggs et al. 1933, p. 769).

Why some persons had sickled cells but not severe
anemia became clearer genetically in the late 1940's,
when James V. Neel from the University of Michigan's
Heredity Clinic demonstrated that sickled cells were not
inherited as a dominant Mendelian characteristic. On the
basis of Taliaferro and Huck’s hypothesis, Neel pointed
out in a 1949 paper, “the inference was that this [domi-
nant] gene was more strongly expressed in some indivi-
duals (sickle cell anemia) than in others (sicklemia [or
sickle cell trait])” (Neel 1949, p. 64). In a 1947 paper

79

reviewing the chemical detection of genetic carriers,
however, Neel had suggested another mode of inherit-
ance: ‘There is present in the colored population a
certain factor which when heterzygous may have no
discernible effects but usually results in sickling, and
when homozygous tends to result in sickle cell anemia”
(Neel 1947, p. 129).

Neel’s interpretation of the inheritance of sickle cell
anemia was generated by his study of another hereditary
blood disorder, thalassemia or Cooley's anemia, a con-
dition which would become significantly linked with
sickle cell research in the 1950s. By the mid-1940s,
clinicians and geneticists knew that thalassemia was
found relatively frequently among persons living in, or
descended from residents of, the Mediterranean coun-
tries, and that the condition could occur in either a
severe or relatively mild form. In 1944, Neel and W. W.
Valentine reported on their investigation of 34 parents,
siblings, or immediate collaterals of three patients with
thalassemia, and one with mild hereditary anemia. From
their genetic and hematologic study, they suggested
that the mild familial anemia was due to a heterozygous
or carrier state, while severe thalassemia resulted from a
homozygous inheritance from two carriers. The mild and
severe forms of the disorder, they proposed, could be
designated as thalassemia minor and thalassemia major
(Valentine and Neel 1944).7

Reasoning from his analysis of thalassemia, Neel
recognized that there was a relatively simple way to
determine whether his hypothesis about the inheritance
of sickle cell anemia was correct. “‘If the homozygous-
heterozygous hypothesis is correct, then both the
parents of any patient with sickle cell anemia should
always sickle. . .If, on the other hand, the disease is due
to a dominant gene with variable expression, only one
parent need sickle, although occasionally, due to the
chance marriage of two sicklers, both parents may
sickle.”” (Neel 1949, p. 64) Thus far, Neel reported, he
had tested 42 parents of 29 patients with sickle cell
anemia for the occurrence of sickling. Although only
13 couples were tested, the results were convincing:
the blood of all 42 parents sickled, “This is the result
expected from the homozgous-heterozygous hypothesis.
On the other hand, the probability of the occurrence
of such a number of positive parents under the variable
dominant hypothesis is (0.76542)*2 or 0.000013"
(Neel 1949, p. 65).%

Reviewing survey data from the U. S. and Africa on
the incidence of sickling, Neel briefly discussed the sub-
ject of gene frequency in sickle cell trait and disease. He
then closed his short paper by noting that, given this
new understanding of the genetic transmission of sickled
cells, one could both accurately predict the disease’s
occurrence and, if so desired, greatly reduce its incidence.

In a genetic situation such as appears to obtain
here, where the heterozygote, who may be termed
the genetic carrier of the disease, may be readily
distinguished from normal and from the homo-
zygote, it is possible to predict with a high degree
of accuracy which marriages should result in
homozygous individuals - in this case, children
with sickle cell anemia. Since (homozygous)
individuals with sickle cell anemia either die young
or, if they reach maturity, have a greatly lowered
fertility, the vast majority of cases of the disease
are the issue of marriages between two (hetero-
zygous) persons with the sickle cell trait. In the
absence of marriage between individuals whose
erythrocytes exhibit the sickling phenomenon,
the frequency of the homozygote would greatly
decrease, and sickle cell anemia would tend to
disappear, with only a very rare case arising as a
result of mutation in a normal individual married
to a person homozygous or heterozygous for the
sickling gene. (Neel 1949, pp. 65-66)

How Cells Sickle: Hemoglobin and the Concept
of Molecular Disease

The chain of researches that would unravel the
puzzling question of how red blood cells sickle, and
in so doing greatly clarify our understanding of how
genes control protein structure, was set in motion on a
spring night in 1945. At the time, chemist Linus Pauling
was serving as a member of the Medical Advisory Com-
mittee that was assisting Vannevar Bush in the prepara-
tion of a report to the President on the state and direc-
tion of science at the close of World War 11. ‘One even-
ing,” Pauling later recalled, “Dr. William B. Castle, Pro-
fessor of Medicine in Harvard University, mentioned to
the other members of the committee the disease sickle-
cell anemia, with which he had had some experience. He
told about the discovery of the disease by Dr. J. B.
Herrick in 1910, and described the characteristic change
in shape of the red corpuscles and the effect of oxygen
in preventing the sickling and of carbon dioxide in
accelerating it" (Pauling 1955, p. 216).

Castle's remarks immediately caught Pauling’s atten-
tion, for in 1935, after studying the structure of rela-

tively simple inorganic and organic molecules for a
decade, Pauling had become interested in the hemo-
blobin molecule.’ Beginning with an analysis of the
structural origin of hemoglobin’s oxygen equilibrium
curve, Pauling and his colleagues at the California
Institute of Technology went on to examine the dena-
turation of hemoglobin and other proteins, and the
magnetic properties of hemoglobin and its derivatives.
For Pauling, long interested in understanding how
molecular structure determines chemical properties,
the study of magnetic properties was ‘‘especially fruitful
in providing information about the nature of the bonds
formed by the iron atoms in hemoglobin with the
neighboring atoms of. . .the globin, and attached mol-
ecules such as the oxygen molecule’ (Pauling 1955,
p. 216).

Pauling thus was well prepared to respond to Castle's
discussion of sickle-cell anemia, particularly his descrip-
tion of Hahn and Gillispie's 1927 experiments on the
effects of oxygen and carbon dioxide on sickling. Paul-
ing suggested to Castle that ‘‘the action of carbon
dioxide was to accelerate the dissociation of oxygen
from oxyhemoglobin. . ., and | pointed out that the
relation of sickling to the presence of oxygen clearly
indicated that the hemoglobin molecules in the red cell
are involved in the phenomenon of sickling.” (Pauling
1955, pp. 216-217)

In 1927 Hahn and Gillispie had recognized that
hemoglobin somehow is involved in sickling. Now, in
1945, Pauling’s agile mind quickly formulated an idea
about the nature of that involvement, an idea triggered
in part by his work on the nature of antigen-antibody
relationships. © “| thought that it was possible that the
patients with sickle-cell anemia manufacture an abnor-
mal sort of hemoglobin molecule, such that the mole-
cules are self-complementary, and stick to one another,
forming long rods, which then line up side by side to
produce a needle-like crystal, which, as it continues to
grow, becomes longer than the diameter of the red cell,
and thus deforms the red cell into an elongated shape.
It was necessary to assume that molecules of sickle-cell
oxyhemoglobin, as well as those of normal adult human
hemoglobin and oxyhemoglobin, do not have this
property of self-complementariness’”” (Pauling 1960,
pp. 2-3).

Pauling, a chemist, recognized the wisdom of collabo-
rating with a physician to explore his new interest in
sickle cell anemia. That collaborator, Dr. Harvey Itano,
arrived at Cal Tech in the fall of 1946 on a three year
American Chemical Society Predoctoral Fellowship in

 
Chemistry. Itano had received his M. D. from St. Louis
University School of Medicine in 1945, where one of his
professors, Dr. Edward Doisy, suggested that he pursue
his interest in chemistry by working with Pauling. Paul-
ing agreed to Doisy’s plan, and in correspondence with
Itano Pauling ‘‘suggested that he investigate the hemo-
globin from the red cells of sickle-cell anemia patients,
in order to see whether it was different from normal
adult human hemoglobin’’ (Pauling 1955, p. 217).

Itano began his hemoglobin research in the fall of
1946 by replicating Hahn and Gillispie's finding that
sickling is prevented by both oxygen and carbon mon-
oxide. He then found that a series of other hemoglobin
derivatives similarly prevent sickling and developed a
diagnostic test enabling physicians to rapidly differenti-
ate between sickle cell trait and sickle cell anemia (Itano
and Pauling, 1949).

Then, with Pauling’s guidance, Itano joined forces
with two postdoctoral fellows, S. J. Singer and A. C.
Wells, to determine whether there were significant
differences in the physical and chemical properties of
hemoglobins from normal adults and from persons with
sicklemia (sickle cell trait) and sickle cell anemia.

Four months after J. V. Neel’s paper in Science,
documenting his hypothesis about the homozygous
inheritance of sickle cell anemia, Pauling, Itano, Singer,
and Wells reported the results of their physical-chemical
researches in the same major journal. They found,
initially, that most of the properties of hemoglobin from
the blood of normal individuals and sickle cell anemia
patients were identical. But then a striking and funda-
mental difference was found, by the painstaking meas-
urement of the different hemoglobins’ electrophoretic
mobility.*!

At the time of their November 1949 report, Pauling’s
group had done electrophoresis studies, each taking 6 to
20 hours, on hemoglobins from 15 persons with sickle
cell anemia, 8 with sickle cell trait, and 7 with normal
blood. “The results,” they announced, “indicate that a
significant difference exists between the electrophoretic
mobilities of hemoglobin derived from erythrocytes of
normal individuals and from those of sickle cell anemic
individuals’ (Pauling et al. 1949, p. 544). Electro-
phoresis of hemoglobin from sickle cell trait carriers
also was found to have a characteristic pattern, one that
looked like the pattern produced by a roughly equal
mixture of normal hemoglobin and sickle cell anemia
hemoglobin. At least electrophoretically, therefore,
“the two components in sicklemia hemoglobin are

identifiable with sickle cell anemia hemoglobin and with
normal hemoglobin’ (Pauling et al. 1949, p. 546).

Based on a further series of ongoing physical-chemical
tests, the Cal Tech researchers reported it seemed
probable that the difference between normal and sickle
cell hemoglobins resided in the globin portion of the
molecule. Their experimental observations, Pauling
and his colleagues judged, thus supported the picture
of the sickling process that Pauling had first envisaged
while talking to William Castle in 1945.

We can picture the mechanism of the sickling
process in the following way [the investigators
wrote in 1949]. It is likely that it is the globins
rather than the hemes of the two hemoglobins
that are different. Let us propose that there is a
surface region on the globin of the sickle cell
anemia hemoglobin molecule which is absent in
the normal molecule and which has a configura-
tion complementary to a different region of the
surface of the hemoglobin molecule. This situation
would be somewhat analogous to that which very
probably exists in antigen-antibody reactions.
The fact that sickling occurs only when the
partial pressures of oxygen and carbon monoxide
are low suggests that one of these sites is very near
to the iron atom of one or more of the hemes,
and that when the iron atom is combined with
either one of these gases, the complementariness
of the two structures is considerably diminished.
Under the appropriate conditions, then, the sickle
cell anemia hemoglobin molecules might be cap-
able of interacting with one another at these sites
sufficiently to cause at least a partial alignment of
the molecules within the cell, resulting in the
erythrocyte’s becoming birefringent, and the cell
membrane’s being distorted to accommodate the
now relatively rigid structures within its confines.
The addition of oxygen or carbon monoxide to
the cell might reverse these effects by disrupting
some of the weak bonds between the hemoglobin
molecules in favor of the bonds formed between
gas molecules and iron atoms of the hemes. (Paul-
ing et al. 1949, pp. 546-547)

At the time their Science paper was published, Paul-
ing, Itano, and their associates recognized that “some of
the details of this picture of the sickling process are as
yet conjectural,’”” awaiting future experimental confirma-
tion or disproval. But if the proposal was correct, they

 
realized that it “‘supplies a direct link between the exist-
ence of ‘defective’ hemoglobin molecules and the
pathological consequences of sickle cell disease’” (Pauling
et al. 1949, p. 547).

With this statement, Pauling introduced his funda-
mentally important concept of sickle cell anemia as a
genetically transmitted molecular disease. Discussing the
genetics of sickle cell disease, Pauling and his co-investi-
gators briefly reviewed Taliaferro and Huck’s dominant
gene theory, and Neel’s recent report of his study
supporting a heterozygous-homozygous mode of inherit-
ance. Then, as investigators are prone to do in the
competitive world of research, Pauling’s group added a
priority claim.'? “Our results had caused us to draw this
inference before Neel’s paper was published. The exist-
ence of normal hemoglobin and sickle cell anemia hemo-
globin in roughly equal proportions in sicklemia hemo-
globin preparations is obviously in complete accord with
this hypothesis’ (Pauling et al. 1949, p. 547).

Pauling, Itano, Singer, and Wells then reached the
core of their paper: an explanation of the probable
relationship between the genetics of sickle cell anemia
and the mechanism of sickling.

In fact, if the mechanism proposed above to ac-
count for the sickling process is correct, we can
identify the gene responsible for the sickling
process with one of an alternative pair of alleles
capable through some series of reactions of intro-
ducing the modification into the hemoglobin mol-
ecule that distinguishes sickle cell anemia hemo-
globin from the normal protein.

The results of our investigation are compatible
with a direct quantitative effect of this gene pair;
in the chromosomes of a single nucleus of a nor-
mal adult somatic cell there is a complete absence
of the sickle cell gene, while two doses of its
allele are present; in the sicklemia somatic cell
there exists one dose of each allele; and in the
sickle cell anemia somatic cell there are two doses
of the sickle cell gene, and a complete absence of
its normal allele. Correspondingly, the erythro-
cytes of these individuals contain 100 percent
normal hemoglobin, 40 percent sickle cell anemia
hemoglobin and 60 percent normal hemoglobin,
and 100 percent sickle cell anemia hemoglobin,
respectively. This investigation reveals, therefore,
a clear case of a change produced in a protein

82

molecule by an allelic change in a single gene in-
volved in synthesis. (Pauling et al. 1949, p. 547;
italics added)

With this statement, Pauling’s group affirmed the
soundness of Dr. James Herrick’s first hypothesis about
the cause of the “‘peculiar’’ sickle-shaped red blood cells
he had first observed under his microscope in 1904:
that some unrecognized change in the composition of
the corpuscle itself may be the determining factor.”
Pauling and Itano’s investigations, part of a sequence of
inquiries into the nature of sickle cell anemia that began
with Herrick’s first case report in 1910, also forged new
links between physical chemistry, human and basic
genetics, and clinical medicine. That fusion would pro-
foundly alter our understanding of the nature of gene
action, and resolve many of the puzzling questions about
allelism that we noted at the beginning of this chapter.
For, in a line of inquiry that at the time seemed far
removed from Beadle, Ephrussi, and Tatum’s basic
genetic researches with Drosophila and Neurospora, the
work of Pauling and his colleagues soon would intersect
with and significantly modify the one gene-one enzyme
hypothesis.

The Molecular Detectives:
Fingerprinting Hemoglobin

While Pauling et al.’s 1949 report provided strong
empirical evidence for the concept of a molecular
disease, it left many questions unresolved and, not
surprisingly, provided a major catalyst for further study.
The torrent of researches on normal and abnormal
hemoglobins since 1949 is suggested by the fact that as
of 1976 some 300 abnormal hemoglobins, in addition
to hemoglobin S (sickle-cell hemoglobin), had been
discovered, and the precise chemical nature of 259 of
these variants had been established (Neel 1976, p. 57).

In the remainder of this chapter, our focus will be
on three interrelated lines of work through the early
1960s that marked the coming of age of ‘“‘molecular
pathology’’ and that, joining with other areas of genetic
research, produced a new understanding of how genes
control the structure of proteins.!3 At the center of
these investigations were two critical questions posed by
the work of Pauling’s group: what is the exact biochemi-
cal nature of the difference between normal and sickle
cell hemoglobin and where in the hemoglobin molecule
is this difference localized?

 
One of the first areas of study to bear fruit after 1949
was the mechanism of the sickling process. In his first
conversation about sickle cell anemia with William
Castle in 1945, and again in his 1949 Science paper,
Pauling had suggested a mechanism for the sickling
process involving the combination of complementary
sites on adjacent hemoglobin molecules, analogous
to the presumed interactions between antigens and
antibodies. With this hypothesis, the known effects of
oxygen and carbon monoxide in reversing sickling were
explained by a disruption of the weak bonds between
the hemoglobin molecules by the bonds formed between
the gas molecules and iron atoms of heme.

The essentials of this picture of the sickling process
were substantiated by 1951 through several lines of
investigation, including further experiments by Pauling
(St. George and Pauling 1951). The principal confirma-
tion of Pauling’s view of the sickling mechanism came
from studies conducted in Boston, Massachusetts and
Cambridge, England. (Fittingly, Dr. William Castle
directed the work of Dr. John Harris in Boston, in
the Thorndike Memorial Laboratories of Boston City
Hospital.) In a 1950 paper, Harris reported on his
study with the polarizing microscope of various con-
centrations of sickle-cell hemoglobin in oxygenated
and deoxygenated states. As Pauling had hypothesized,
Harris found that the deoxygenated hemoglobin formed
spindle-shaped bodies arranged as tactoids. This forma-
tion, Harris explained, “‘is evidence of a specific arrange-
ment or linkage of the individual molecules with the
formation of long chains of hemoglobin elements. . .”
(Harris 1950, p. 199).

At first independent of Harris’ work, although the
two groups later corresponded about their findings,
comparable studies were initiated at the University of
Cambridge's Cavendish Laboratory by noted protein
crystallographer F. M. Perutz. Perutz had spent some
10 years collecting x-ray diffraction data from hemo-
globin crystals in an effort to map the protein's three-
dimensional structure, when in 1950 his attention
was directed to sickle cell anemia by Dr. F. Eirich,
from the Polytechnic Institute in Brooklyn, New York.
Then, following up on a suggestion by Dr. C. A. Stet-
son of the Rockefeller Institute, Perutz and Mitchison
reported in 1950 that their solubility studies of normal
and sickle cell hemoglobin, using a polarizing micro-
scope, indicated that ‘‘the reduced [deoxygenated]
hemoglobin in sickle cells is in a crystalline state”
(Perutz and Mitchison 1950, p. 678). Several months

later Perutz reported on further studies, using x-ray
diffraction to see whether there were any obvious
structural differences between sickle-cell anemia and
normal oxyhemoglobin molecules. But the nature of
the molecular differences between normal and sickle
cell hemoglobin was not to be revealed by x-ray dif-
fraction. “As to the structural differences between
normal and sickle-cell anemia haemoglobin, our crys-
tallographic results provide no clue, but merely serve
to emphasize the close similarity between the two
proteins.” To Perutz and his collaborators, ‘‘this was
a most surprising result, considering that normally
two related but slightly different proteins - for example
the haemoglobins of closely related animal species

have totally different crystal structures’’ (Perutz,
Liquori, and Eirich 1951, pp. 931, 929).1%

Another line of attack on the problem of localizing
the structural basis for sickled cells was undertaken
by the eminent hemoglobin researcher W. A. Schroeder.
Working with A. M. Kay and A. C. Wells, Schroeder's
approach to the molecular disease puzzle was to see
whether there were differences in the amino acid con-
tent of hemoglobins from blacks with and without sickle
cell anemia. Their results, like Perutz’s x-ray diffraction
studies, were largely negative, for comparative analysis
indicated no significant differences in the basic and
acidic amino acid content of normal adult and sickle cell
hemoglobin. Slight differences, however, were detected
in the two hemoglobins’ content of four uncharged
amino acids. Perhaps, Schroeder suggested, these differ-
ences might affect the folding or coiling of the polypep-
tide chains so as to change the acid or base content of
other amino acid groups, and thus indirectly alter the
electrophoretic properties of the hemoglobins (Schroe-
der, Kay, and Wells 1950).

Schroeder's work, like other researches at the time,
proceeded on the basis of Pauling’s suggestion that the
structural differences between hemoglobins A (normal)
and S (sickle-cell) lay in the globin portion of the mole-
cule. The correctness of this assumption was demon-
strated in 1952 by Havinga and Itano in Pauling’s labora-
tory. By separating the heme from the globin and sub-
jecting the globin portions to electrophoresis, they
found that the globins had the same differences in
electrophoretic mobility as did the whole hemoglobin A
and S molecules (Havinga and Itano 1952). In a series of
concurrent experiments, Havinga ruled out a variety
of possible reasons for differences between hemo-
globins S and A, including optical rotation, phosphorus

 
content, and the number of terminal acid residues
(Havinga 1953).

The effort to locate the structural difference that
accounted for normal and abnormal hemoglobin mole-
cules was further complicated between 1950 and 1953
as clinical geneticists, led by James V. Neel and Harvey
Itano, discovered three more abnormal varieties of adult
human hemoglobin, named in alphabetical order hemo-
globins C, D, and E. These newly recognized abnormal
hemoglobins, the researchers quickly found, could mani-
fest themselves alone, or in synergistic interaction with
sickle cell anemia, or with thalassemia (see note 7).
Still another disease, they found, could result if an
individual simultaneously- had the sickle cell and the
thalassemia minor traits. Thus, by 1953, Itano was able
to review ten distinct hereditary clinical states associated
with abnormal hemoglobin metabolism (Itano 1953;
see also reviews by Itano 1955, Pauling 1955). For both
clinical and basic researchers in genetics, biochemistry,
and physical chemistry, there was now an almost bewil-
dering array of molecular hemoglobin disorders with
which to work. In terms of the central questions raised
by the molecular disease concept, that of where and
how the hemoglobin molecules differed structurally,
researchers focused principally on hemoglobins A, S, and
C. If structural differences could be pinpointed research-
ers knew they would gain a critical insight into ‘a funda-
mental question in biochemical genetics:”" “whether or
not the abnormal hemoglobin genes are alleles, that is,
whether mutations resulting in the alteration of hemo-
globin. metabolism takes place at one or more than one
chromosomal locus’ (lItano 1955, p. 293). In 1949, we
recall, Pauling et al. had postulated that the genes for
hemoglobins A and S were allelic, and, with the disco-
very of hemoglobin C in 1950 by Itano and Neel, a
series of studies soon “furnished strong biochemical and
genetic evidence that the genes for hemoglobins S and
C are allelic or closely linked” (ltano 1955, p. 293).

Through the early 1950s, the varied attempts to
locate the structural difference between normal and
sickle cell hemoglobin, beyond implicating the globin
portion of the molecules, had served primarily to rule
out a series of possibilities. The one viable hypothesis
seemed to be Schroeder et al.'s suggestion that the
molecules might be composed of the same polypeptide
chains, but folded in different ways. “The interesting
possibility exists,” said Pauling in his 1955 Harvey
lecture, “that the gene responsible for the sickle-cell
abnormality is one that determines the nature of the

folding of polypeptide chains, rather than their com-
position’’ (Pauling 1955, p. 222).

A little over a year after Pauling’s Harvey lecture,
the baffling problem of the specific chemical difference
between hemoglobins A and S began to be resolved by
the researches of a young protein chemist, Vernon M.
Ingram, working in Perutz’s laboratory. Although only
two decades have elapsed since Ingram’s first paper, the
strides that have been made in analyzing the sequential
and spatial structure of proteins make it difficult to
appreciate today the problems facing protein chemists
in the mid-1950’s and the corresponding elegance of
Ingram’s work. Proteins are extremely complex macro-
molecules, and in the early 1950s little was known
about the exact sequences in which given amino acids
form given proteins, much less about the relationships
between sequencing and the three-dimensional shapes
of a protein's polypeptide chains (see note 14). After
years of arduous work, biochemist Frederick Sanger
finished the first complete sequence analysis of a protein
in 1953, an achievement that ‘‘contributed decisively
to the proof of the peptide theory’ - the long debated
theory that protein molecules are built of chains of
amino acids bound together by peptide bonds (Fruton
1972, p. 148). The protein he studied was the hormone
insulin, a relatively small protein whose longest polypep-
tide chain contained only 51 amino acids. Complex as
the sequence analysis of insulin’s structure proved to be,
hemoglobin presented a far more formidable task, for,
with a molecular weight of about 65,000, researchers
knew it would probably contain about 600 amino acid
residues.

Vernon Ingram arrived at the Cavendish Laboratory
in 1952, to join in Perutz’s x-ray crystallography studies
of hemoglobin crystals. Then, Ingram recalls, “about
the same time as the Watson-Crick breakthrough in
the same lab, | went off in a slightly different direction
from Perutz and began to study the relationship between
the heme group and its adjacent polypeptide chains’
(Ingram, personal communication). Ingram'’s interest in
sickle cell hemoglobin was aroused in 1955 by the arrival
at Cavendish of an Oxford physician, A. C. Allison.
Allison was one of a number of clinicians then investigat-
ing both the incidence of sickle cell trait and disease in
Africa, and the hypothesis proposed by Brain in 1952
that the evolutionary significance of hemoglobin S might
lie in its conferring protection against malarial parasites
(Brain 1952; Allison 1954; Pauling 1955). Allison also
became interested in the formation of hemoglobin crys-

 
tals in sickle cells, and came to the Cavendish to do
fiber x-ray crystallography studies. Given the state of
fiber x-ray techniques at the time, Ingram remembers,
Allison ‘““didn’t get any significant x-ray pictures,’” and
departed leaving behind some of his sickle cell hemo-
globin samples. But Allison’s visit to the Cavendish
would prove highly significant in other respects, for it
‘was the quite fortuitous appearance of those sickle cell
samples’’ which triggered Ingram’s idea of looking at
their protein chemistry (Ingram, personal communica-
tion). It was not, of course, completely fortuitous. For
Ingram, working “‘in a lab which was passionately inter-
ested in anything to do with hemoglobin,” was familiar
with the research of Pauling’s group and with the sub-
sequent attempts to determine the difference between
hemoglobins A and S.

When Ingram decided that he, too, would seek to
uncover how the protein globins of normal and sickle
cell hemoglobins differed, he knew from previous
investigations that the difference, whatever it was, must
be a small one. He knew, too, that the hemoglobin
molecule was too large for the type of complete se-
quence analysis of insulin that Sanger had performed.
Faced with this reality, Ingram devised a short cut,
utilizing a combination of methods that enabled him to
obtain and analyze relatively small peptide fragments
from the whole molecule. In the mid-1950s, one of the
newest and most reliable ways of separating peptides
and amino acids was by means of the enzyme trypsin,

which split polypeptide chains by specifically degrading .

the chemical bonds formed by the carboxyl groups of
two amino acids, lysine and arginine. Other studies of
hemoglobin’s amino acid composition had indicated
that there were some 60 of these particular carboxyl
groups in hemoglobin A and S molecules. But, because
Perutz’s x-ray diffraction analysis had indicated that
each hemoglobin molecule was composed of two identi-
cal “half molecules,”” Ingram anticipated that “the
number of peptides obtained by the action of the
trypsin should be about thirty, an average chain-length
of ten amino-acids. Small differences in the two proteins
[hemoglobin A and S], he reasoned, will result in small
changes in one or more of these peptides’ (Ingram
1956, p. 793).

To try to detect these small differences, Ingram
ingeniously combined paper electrophoresis and the
paper chromotagraphy methods that he had watched
Sanger use. By this combination he created a two-
dimensional method that enabled him to comparatively
“fingerprint” the hemoglobin S and A fragments he

obtained from the tryspin digest. The fingerprints
revealed approximately 30 peptide spots, confirming
Perutz’s view that the human hemoglobin molecule
consists of two identical half molecules. As he also had
expected, Ingram saw that the normal and sickle cell
globins contained the same number of peptides. But
the fingerprints did what other attempts to locate a
difference between the S and A globins had been unable
to do - they revealed a small difference in the largely
identical molecules. As Ingram reported in 1956, “. . .
there is one peptide spot clearly visible in the digest of
haemoglobin S which is not obvious in the haemoglobin
A ‘finger print’ (Ingram 1956, p. 793).

Prior to the development of Ingram’s fingerprinting
method, it had been impossible to decide whether the
small but critical difference between hemoglobins A
and S resided in the amino acid sequences of the poly-
peptide chains, or in the ways those chains were folded.
But by means of the trypsin digest and fingerprinting,
as Ingram concluded in his short paper:

One can now answer at least partly the question
put earlier, and say that there is a difference in
the amino-acid sequence in one small part of one
of the polypeptide chains. This is particularly
interesting in view of the genetic evidence that the
formation of haemoglobin S is due to a mutation
in a single gene. It remains to be seen exactly how
large a portion of the chains is affected and how
the sequences differ. (Ingram 1956, p. 294)

Ingram’s experiment thus had opened a new vista in
biochemical genetics and protein chemistry, providing
the way to show with detailed precision the relationship
between a gene and the protein under its control. Less
than a year after his first paper, Ingram published a
second short report in which he answered his 1956
question of “how large a portion of the chains is affected
and how the sequences differ.”

| have now found that out of nearly 300 amino-
acids in the two proteins, only one is different;
one of the glutamic acid residues of normal haemo-
globin is replaced by a valine residue in sickle cell
anaemia haemoglobin. The latter is an abnormal
protein which is inherited in a strictly Mendelian
manner; it is now possible to show, for the first
time, the effect of a single gene mutation as a
change in one amino-acid of the haemoglobin
polypeptide chain for the manufacture of which
that gene is responsible. (Ingram 1957, p. 326)

 
Vernon Ingram had detected the basis for the inher-
ited molecular disease, sickle cell anemia. It was, he had
shown, caused by the smallest possible alteration in the
large hemoglobin molecule: the substitution of a single
amino acid, glutamine, by another, valine. The technique
of protein fingerprinting, as Ingram realized, had simply
and decisively answered one of the most intriguing
questions in the explosive new field of molecular ge-
netics, that of precisely how a gene mutation affects
the specific structure of a protein.

What, then, was the nature of the mutation within
the hemoglobin gene that produced this small but signifi-
cant alteration in the structure of the hemoglobin mole-
cule? Presumably, Ingram wrote in 1957, it is an equally
small change in the hemoglobin gene. “It is not known,
but it may well be that this involves a replacement of
no more than a single base-pair in the chain of the
deoxyribonucleic acid of the gene” (Ingram 1957,
p. 327). This hypothesis about a human gene and its
protein, Ingram pointed out, accorded well with the
new knowledge of genetic subunits being gained from
the standard organisms of molecular geneticists, Neuro-
spora, Aspergillus, and bacteriophage.

The results presented in this communication are
certainly what one would expect on the basis of
the widely accepted hypothesis of gene action;
the sequence of base-pairs along the chain of
nucleic acid provides the information which
determines the sequence of amino-acids in the
polypeptide chain for which the particular gene,
or length of nucleic acid, is responsible. A sub-
stitution in nucleic acids leads to a substitution
in the polypeptide. (Ingram 1957, pp. 327-328)

Less than a month after Ingram’s 1957 paper, another
important report issued from Pauling’s laboratory.
Perutz’s x-ray crystallography studies and Ingram’s
fingerprint had led them to conclude that the hemo-
globin molecule consisted of two identical ‘’half mole-
cules.” Now, on the basis of complex quantitative chem-
ical analysis, H. L. Rhinesmith, W. A. Schroeder, and
Pauling had succeeded in identifying the number and
kind of polypeptide chains in normal adult hemoglobin.
The globin, they determined, consists of two sets of
polypeptide chains, or a total of four chains forming
two identical half molecules (Rhinesmith, Schroeder,
and Pauling 1957). With this report, there was now a
solid line of evidence, derived from a complex human
protein, that confirmed and greatly refined the concept

 

of gene action generated in 1908 by Sir Archibold
Garrod’s study of inborn errors of metabolism - that of
a one-to-one relationship between genes and enzymes.

That concept, as we have seen, had been rediscovered
and reenunciated as the one gene-one enzyme hypothesis
by George Beadle and his associates in the 1930's and
early 1940's, through their biochemical genetic re-
searches with Drosophilia and Neurospora. Ingram
recalls that while he was at the Cavendish laboratory
from 1952-1958 the one gene-one enzyme hypothesis
was “well accepted’’ by himself and his colleagues, so
that he promptly saw the “‘sickle cell hemoglobin busi-
ness’’ as providing a ‘direct illustration’’ of the correct-
ness of Beadle et al.'s formulation (Ingram, personal
communication). But acceptance of the one gene-one
enzyme hypothesis was far from universal among genet-
icists from the early 1940's through the mid-1950’s, in
part because, like Garrod’s explanation, it seemed too
simple an account of gene action.

There were, of course, other reasons besides its
simplicity for the slow acceptance of the one gene-one
enzyme concept and all that it implied.

It would take some years to understand the
relationship between mutations and enzymes,
primarily because so little was known concerning
the structure of proteins at the time there was so
much discussion of the one gene-one enzyme
concept. We may have difficulty in appreciating
the problem unless we keep in mind that the
concepts were formulated without any clear
idea of the properties of proteins which conferred
specificity. . .Although proteins were known to be
composed of polypeptide chains which were
assumed to be folded in specific ways, there was
no clear concept of what determined the sequence
of amino acids or whether the sequence was
related to the three-dimensional shape. Did genes
control the specificity of enzymes and if so how?
If a mutation changed an enzyme activity was it
because the protein was changed or produced in
smaller amounts? Would the mutation of one gene
change more than one protein? Could genes
mutate in a variety of ways?

Without a clear concept of the nature of the gene
or of its supposed product, a specific protein,
little progress could be made. Geneticists could
study the phenotypes produced by mutation as
had been done for years. The improvement pro-
vided by Neurospora, which could be grown in a
simple, completely defined medium, was that the
change in phenotype could be defined much more
precisely in chemical terms. In an attempt to
simplify the problem, the question was put in the
following form. Do any genes have a single pri-
mary function and if so what proportion of muta-
tions produces changes of this nature? (Taylor
1965, pp. 4-5)

With this precis of the questions rampant in genetics
through the early 1950s, the impact of the researches on
sickle cell hemoglobin is apparent. By 1957, principally
through the researches of Ingram and of Pauling’s group,
geneticists knew that a mutant hemoglobin gene pro-
duced a disease by altering the presence of a single
amino acid in the polypeptide chain of the hemoglobin
molecule. The one gene-one enzyme concept of gene
action had been essentially correct. But it had been too
simple, because enzymes are proteins, but not all pro-
teins are enzymes. Principally through research from
many quarters on the nature of hemoglobin, it was
gradually recognized that structural proteins, too,
might be the direct products of gene action, and the
one gene-one enzyme hypothesis was recast in terms of
one gene-one protein. Then, the trail of researches into
the nature of sickle cells, that began in 1910 with Her-
rick’s first clinical report, revealed the specificity of gene
action within a protein, and one gene-one protein was
recast as one gene-one polypeptide. “Thus,” wrote
Bentley Glass on the centennial of Gregor Mendel’s
publication, ‘‘geneticists were led to the conclusion
that, as predicted from the Watson-Crick model of the
DNA molecule, the sequence of nucleotides in the DNA
molecule specifies the sequence of amino acids in the
polypeptides’ (Glass 1965, p. 234).

Another core aspect of gene action elucidated by the
study of abnormal hemoglobins was allelism. As we have
seen, Ingram’s fingerprints of hemoglobins A and S pro-
vided strong indirect support for the supposition ad-
vanced initially by Pauling et al. in 1949: that the
mutant gene responsible for sickle cell hemoglobin is
an allele or variant of the normal hemoglobin gene,
occupying the same chromosomal locus. As we also
mentioned, the rapid discovery of other abnormal
hemoglobins, beginning with the identification of
hemoglobin C in 1950, raised new questions about
allelism: were hemoglobins C, D, E, and so on, like
hemoglobin S, due to another allele at the same locus,
or did it represent a new mutational system at an inde-

pendent locus? The first answers to this fundamentally
important question, once again, were provided by
Ingram’s fingerprints.

In 1951, shortly before Ingram moved from Cam-
bridge, England to MIT in Cambridge, Massachusetts,
he and J. A. Hunt published a short note in Nature:
“Allelomorphism and the Chemical Differences of the
Human Hemoglobins A, S and C.” By preparing finger-
prints of hemoglobin C and comparing them with their
analysis of the A and S fingerprints, Hunt and Ingram
had found that C was caused by a different amino acid
substitution at the same site in the polypeptide chain as
the A and S variation. While hemoglobin S was produced
by the substitution of valine for glutamine, hemoglobin
C occurred when the same glutamic acid residue was
replaced by lysine.

“These results,” wrote Hunt and Ingram, “have
interesting genetic implications.”

They are the first steps in a search for a correlation
between the linear fine structure of a gene such as
that determined recently by Benzer and Ponte-
corvo, and the linear structure of the polypeptide
chain of the protein the synthesis of which that
gene controls. . .

Our results also shed light on the position of these
two mutations on the haemoglobin gene or genes.
Genetic evidence shows that the haemoglobin S
and C mutations are allelic or occur at linked sites;
but the statistical evidence is not sufficiently
strong to distinguish between these two possibili-
ties. If we assume a direct relationship between the
internal (linear) structure of the gene, and the
linear arrangement of the amino-acid residues in
the haemoglobin molecule, then the finding that
the same amino-acid residue, glutamic acid, is
altered in both mutations implies that they are
indeed allelic mutations and occupy the same site
on the gene. Thus if these ideas are correct the
chemical investigation of proteins such as the
human haemoglobins can provide a powerful,
though indirect, tool to help the geneticist in
mapping the positions on the gene where certain
mutations occur.

In order to obtain sufficient statistical data and a
sufficient number of mutants, such a programme
must eventually turn to proteins from micro-
organisms. However, it is hoped that the abnormal
human haemoglobins will provide a few mote

 
useful examples of the effects of gene mutations
on protein structure. (Hunt and Ingram 1958,
pp. 1062-1063; see also Hunt and Ingram 1960)

Hunt and Ingram’s modest hope that abnormal
human hemoglobins would provide ‘a few more useful
examples’ of the effects of gene mutations on protein
structure has been amply realized in the years since
1958. The study of inherited hemoglobin abnormalities
has provided the clearest evidence that similar traits
are often determined by multiple alleles of a single
locus. A 1971 text, for example, noted that over 175
“hereditary abnormal hemoglobin’ diagnoses had been
made, and had been traced to variations or alleles in
only five loci. “Remarkably,” the authors wrote, ‘‘one
of the clearest demonstrations’’ of the existence and
effects of multiple alleles ‘‘has come from a human
character: the variations in the polypeptide chains
that make up the globin portion of the hemoglobin
molecule.” (Levitan and Montagu 1971, p. 551)

The Lesson of Rare Maladies

The study of abnormal hemoglobins, which now
number some 300, is a continuously unfolding one,
involving interactions between many areas of clinical
and basic research. We have looked at one portion of
that study, the trails of inquiry that led from the discov-
ery of strangely elongated and sickle-shaped red blood
cells to new knowledge of how normal and mutant
genes govern the structure of proteins. This particular
path from clinical to basic knowledge, of course, was
neither straight not simple. The definition and elucida-
tion of sickle cell anemia as a molecular disease built
upon decades of prior researches into the nature of
hemoglobin, and, as we have seen, human and basic
geneticists, crystallographers, physical chemists and
biochemists, were among those whose often collabora-
tive researches converged to unravel the genetic prin-
ciples contained in normal and abnormal hemoglobin
molecules, and to link their findings with those from
other areas of molecular genetics.

To Dr. Vernon Ingram, reflecting in 1976 on the
history of hemoglobin research in which he has played
such a central role, it is not surprising that “‘the study
of human or animal diseases will frequently and unpre-
dectably lead to fundamental insights into basic mecha-
nisms in biology.” But to Ingram, what happened in
the arena of molecular genetics was and is surprising.
“The coming field in the molecular biology of genetics

in the middle 1950s was bacterial and viral genetics,”
Ingram said. “So if somebody, say in 1955, had pre-
dicted from which field would come the first demonstra-
tion that one gene difference is related to results in a
specific localized difference in a protein, they would
have said from bacterial or viral materials. We were as
surprised as anyone else that it in fact happened to come
from a human protein’ (Ingram, personal communica-
tion).

Today, two decades after that “‘surprising’’ event,
the study of hemoglobin abnormalities continues to
weave between and impact upon clinical and basic
research. “The study of the abnormal hemoglobins,”
James V. Neel wrote in a volume of bicentennial essays
on advances in American medicine, “*has not only pro-
duced a paradigm for ‘molecular’ diseases in general,
but has yielded insights into the fine details of chromo-
some structure in mammals which would not otherwise
be available’’ (Neel 1976, p. 60).

 
 

Chapter 5
NOTES

1. The explosive growth of knowledge generated by mole-
cular biology has revealed Mendel’s ‘‘characters’’ or units of
heredity to be segments of DNA molecules. Through the inter-
mediary activities of RNA, these DNA segments or genes serve
as indirect patterns for the reproduction of polypeptides, chains
of amino acids which are, or combine to form, proteins. ‘Thus,
overall, the gene (DNA) clearly specifies the protein. But with-
out proteins, DNA cannot be made; without RNA, proteins
cannot be made. Molecular biology is a drama with these as the
three major actors, each owes its existence to the others’’ (Hand-
ler 1970, p. 15).

2. In the second edition of /nborn Errors (1923), Garrod
reported that evidence for the correctness of his hypothesis had
been provided in 1914 by Gross, who reported finding in normal
blood plasma but not in the plasma of alkaptonurics an enzyme
that oxidized homogentisic acid. Gross’ finding, however, was
never replicated, and it was not until 1958 that this hypothesis
was confirmed by LaDu and his associates, who demonstrated
the absence of the enzyme in liver biopsy specimens from an
alkaptonuric patient (Glass 1965, p. 231).

3. This failure is amply illustrated by the 1942 book, New
Paths in Genetics, authored by the eminent J. B. S. Haldane.
For, as Glass points out:

. . .Haldane, of all geneticists of his time, was best trained
in biochemistry and most open to see its genetic signifi-
cance. Yet the book is singularly lacking in analyses of
possible gene-enzyme relationships. Garrod’s work of
1923 is cited for its example of human metabolic abnor-
malities inherited as simple recessives; the relationship of
phenylketonuria and alkaptonuria to blockage of specific
steps in amino acid metabolism is implicitly, but not
explicitly, recognized, but the enzymatic relationship is
scarcely hinted at. (Glass 1965, p. 232)

Unawareness of Garrod’s work, in turn, is exemplified by Beadle
and Tatum’s opening sentence in their now classic 1941 paper,
"Genetic Control of Biochemical Reactions in Neurospora.’

From the standpoint of physiological genetics the devel-
opment and functioning of an organism consist essentially
of an integrated system of chemical reactions controlled
in some manner by genes. It is entirely tenable to suppose
that these genes which are themselves a part of the sys-
tem, control or regulate specific reactions in the system
either by acting directly as enzymes or by determining the
specificities of enzymes.” (Beadle and Tatum 1941,
p. 499)

In their first reference Beadle and Tatum then note that “‘the
possibility that genes may act through the mediation of enzymes
has been suggested by several authors,’” and they refer the reader
to publications by Troland (1917), Wright (1927), and Haldane
(1937) for discussion and further references.

4. "The idea was simple,’” George Beadle has stated.

‘Select an organism like a fungus that has simple nutritional
requirements. This will mean it can carry out many reactions by
which amino acids and vitamins are made. Induce mutations by
radiation or other mutagenic agents. Allow meiosis to take place
so as to produce spores that are genetically homogeneous. Grow
these on a medium supplemented with an array of vitamins and
amino acids. Test them by vegetative transfer to a medium with
no supplement. Those that have lost the ability to grow on the
minimal medium will have lost the ability to synthesize one or
more of the substances present in the supplemented medium.
The growth requirements of the deficient strain would then be
readily ascertained by a systematic series of tests on partially
supplemented media.

“In addition to the above specifications we wanted an
organism well-suited to genetic studies, preferably one on which
the basic genetic work had already been done.”’ (Beadle 1964,
p.594)

5. Hahn and Gillispie's gas chamber experiments fell into
disrepute during the 1930's because other investigators had
trouble replicating their findings. In 1940, however, |. S. Sher-
man reported that, using similar methods, he could distinguish
experimentally between sickle cell trait and sickle cell anemia,
based on the amount of oxygen tension needed to produce
sickling (Sherman 1940).

6. The term “homozygous’’ means that an organism has
inherited identical genes at a given locus, while ““heterozygous’’
refers to the possession of different alleles at a given locus.
Thus, in the case of sickle cell hemoglobin, a homozygous
person, who has sickle cell disease, has inherited the sickle cell
hemoglobin gene (hemoglobin c), from both parents; the person
with sickle cell trait, who is only a carrier of the disease, is
heterozygous, having a normal or hemoglobin A gene and its
allelic hemoglobin S gene at the same locus.

7. The thalassemias, too, provide an excellent illustration of
the ways that a clinical disorder can generate and interact with
fundamental research. Much like sickle cell anemia, study of
the thalassemias has produced more detailed knowledge both of
‘molecular diseases,” and of the mechanisms involved in the
genetic control of protein structure. Thus, as a 1976 review
article noted, ‘‘the thalassemia literature abounds with syn-
dromes that mix classical and molecular genetics with clinical
hematology’’ (Orkin and Nathan 1976, p. 710). From this some-
times confusing mix of inquiries, researchers have found that
thalassemia syndromes are caused by deficient production of
specific polypeptide chains. Unlike sickle cell anemia, the globin
chain in thalassemias, when it is not absent, is structurally
normal. Genetically, therefore,

the abnormality in the thalassemias must involve either
the globin genes themselves or regulatory elements
closely linked to them. Newer technics in cellular and

 
molecular biology have been applied to the study of each
phase of gene expression from the DNA, to the trans-
cribed messenger RNA’s (mMRNA's), to protein synthesis
utilizing globin mRNA’s as templates to define the
molecular defects in the thalassemia syndromes.

In one sense the thalassemias are all quite similar in
that the defect in globinchain synthesis can always be
traced at least to the level of the globin MRNA's. (Orkin
and Nathan 1976, p. 711)

8. As occurs frequently in science, recognition of the correct
mode of inheritance of sickle cell anemia was a case of ‘‘simulta-
neous discovery,” for which history has largely credited only one
discoverer. In 1949, independent of Neel’s work, a British
physician named E. A. Beet, who had been studying the inci-
dence of sickle cell trait and disease in East Africa also recog-
nized the heterozygous-homozygous mode of inheritance (Beet
1949).

9. The human red blood cell or erythrocyte is nearly all
hemoglobin, 95% of the dry weight of the cell. Due to the high
concentration of hemoglobin in the cell, and the corresponding
lack of such usual cellular components as a nucleus, hemoglobin
is easily isolated and had been a favorite subject for protein
research since the second half of the 19th century. When Pauling
turned his attention to the hemoglobin molecule in 1935, chem-
ists knew that the molecule consisted of four heme or iron-
containing groups with which oxygen combines to form oxy-
hemoglobin, and globin, a bulky protein in which the heme is
“imbedded.” At the time, little was known about the detailed
structure of the globin portion of the molecule.

10. For a discussion of antigen-antibody theory and research,
including Pauling’s own work on this topic, see Chapter 6.

11. Pauling and his colleagues, in 1949, were able to utilize a
highly sophisticated form of electrophoresis, a technique which
permits the measurement of the physical properties of molecules
such as hemoglobin, recording characteristic patterns that enable
one to identify different molecules or chemical substances.
Electrophoresis, for example, can distinguish two different
proteins as follows: the proteins are placed in an electric field,
with a positive and negative side; proteins have positive and
negative surface charges, which causes positively charged pro-
teins to migrate to the negative pole of the electrophoretic field,
at a rate depending on the strength of the positive charge. Con-
versely, a negatively charged protein moves to the positive pole
of the field. Hemoglobin electrophoresis had first been per-
formed in 1939, by B. D. Davis and E. J. Cohn.

12. As documented by historians and sociologists of science,
priority disputes are a frequent and characteristic accompani-
ment of research, for reasons that are understandable in terms of
the values and the rewards of scientific research. For the classic
sociologic study of priority disputes, see Merton 1957.

13. Among the many and significant areas of hemoglobin
research that we will not touch upon are work on the evolution
of proteins, the differences between fetal and adult hemoglobins,
and chromosomal relationships of hemoglobin loci. For a succint
but comprehensive review and bibliography of these and other
aspects of hemoglobin research, see Neel 1976.

90

14. The difficulties can be appreciated when one realizes that
“proteins are immensely complex macro-molecules since they
are polymers built up from 20 different building blocks (the
amino acids). Thus the organic chemist must determine both
how the amino acids are linked together and what their order is
within a given linear polypeptide chain. Likewise, the biochemist
wishes to know both how the backbone linkages are connected
and what trick is used to order the amino acids during synthesis
. . .Aside from the question of sequence, there is also the prob-
lem of how polypeptide chains assume their final 3-D configura-
tions. The correct functioning of almost all proteins depends not
only upon possession of the correct amino acid sequence but
also upon their exact arrangement in space’ (Watson 1965,
pp. 169-170).

15. One such line of biochemical evidence was offered in
1954 by clinical geneticist and biochemist |. Herbert Scheinberg
and his associates, from the New York State Psychiatric Institute
and Columbia University’s College of Physicians and Surgeons.
Using a new experimental method, paper electrophoresis, Schein-
berg’s group sought to identify the chemical basis of the known
differences in the positive electrical charges between hemo-
globins A, S, and C. Their experiments provided soon widely
cited evidence ‘that the difference in charges between hemo-
globins a, [s], and c are due to differences in their content of
free carboxyl groups.”’ But, they acknowledged, ‘the structural
basis for the apparent difference in the content of free carboxyl
groups of these hemoglobins remains obscure’’ (Scheinberg,
Harris, and Spitzer 1954, pp. 779, 782).

16. George Beadle remembers that:

“In 1945 | held a Sigma Xi National Lectureship under
which | gave lecures on biochemical genetics and the
one gene-one enzyme interpretation. | was much im-
pressed with the resistance to this notion, especially in
agricultural colleges where workers were familiar with the
genetics of such characteristics as egg production, and
milk production in dairy cattle. They were sure gene
action could not be generally described in the simple
way we had postulated. It seems to me the status of the
concept dropped to an all-time low at the Cold Spring
Harbor Symposium of 1951. In rereading the volume on
those meetings, | have the impression that the number
whose faith in one gene-one enzyme remained steadfast
could be counted on the fingers of one hand - with a
couple of fingers left over’’ (Beadle 1966, p. 30).

 
Chapter 5
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CHAPTER 6
A CRUCIAL EXPERIMENT OF NATURE: MULTIPLE MYELOMA
AND THE STRUCTURE OF ANTIBODIES

Over the past century, beginning with efforts of
medical bacteriologists to find ways of protecting man
and his domestic animals from the ravages of infectious
diseases, the field of immunobiology has involved a
steadily broadening scope of inquiry. From many
disciplines, approaches, and interests, clinical and
laboratory investigators have gradually defined and are
seeking to understand the three key features of the
phenomenon called immunity: recognition, specificity,
and memory. That is, first, how does the immune system
“recognize’’ potentially hazardous foreign antigens, and,
of equal import, recognize the body's own constituents
as harmless? Or, in the words of Burnet, how does the
immune system distinguish between ‘not self’ and
“self?” The immune system, secondly, operates with
remarkable specificity against millions of chemically
different antigenic structures. Thus, closely related to
understanding how recognition occurs, immunobiol-
ogists want to know how the immune system produces
a specific antibody against any one of millions of anti-
gens. The third key characteristic of the immune system
is ““memory:’’ how, days or years after its first exposure
to an antigen, is an organism able to ‘‘remember’’ that
exposure and react more rapidly and strongly to a
second encounter?

Finding answers to these questions, investigators have
long realized, has obvious medical significance. And, as
has become increasingly evident in recent years, the
quest to understand how immune defense mechanisms
operate also has led us into the “central regions’ of
biology. “The current explosion in immunological
research,” as Lewin pointed out in 1974,

throws out waves of discoveries that are giving
insights into the science undreamed of a few years
ago. Immunobiology is now one of the most
rewarding and promising areas of biological
research. It is rewarding because it spreads into
many areas of acute social misery giving prospects
of long-hoped-for cures: the successes of vaccina-
tions against many bacterial and viral infections
may soon be followed by assaults on cancer and

diseases such as rheumatoid arthritis and the
presently unassailable parasitic infections; immu-
nology also holds the key to safe organ transplan-
tations. And it is promising because the drive
toward understanding the molecular mechanisms
behind the immune responses is certain to reveal
features fundamental to the whole of biology.
(Lewin 1974, p. 2)

During the relatively brief span of its existence, the
field of immunobiology has become so vast, and the
lines of disease-oriented and basic research pursued with-
in its compass so complex and intertwined, that no one
book could pretend to be a definitive history. Within the
even narrower scope of a single essay, we will look at
only a single but critical strand in the history of immu-
nology, a strand that exemplifies how ‘‘major thrusts
toward fundamental progress in immunobiology have
been guided by questions formulated from experiences
in the clinic’’ (Bach and Good 1972, p. xiii). These
clinical problems, in the main, have centered around
what immunologist Robert Good has termed ‘the
crucial experiments of nature,” a series of diseases which
have “contributed maximally to the development of our
modern concepts of immunology’’ (Good 1972, p. 23).

The particular disease problem that we will examine
is multiple myeloma, a relatively rare form of cancer
that accounts for only some 0.5 percent of all malig-
nancies and about two deaths per 100,000 persons per
year. But although a rare form of cancer, multiple
myeloma ‘‘probably represents the most important of
all experiments of nature’’ for immunobiologists (Good
1972, p. 25). For, as a trail of medical and scientific
research has revealed since the first case of multiple
myeloma was documented in 1846, this cancer is a
tumor of the plasma cells which are responsible for the
production of antibodies. In patients with multiple
myeloma, as we shall learn, the immune system's protein
metabolism is so altered that the excretion of certain
abnormal proteins is a hallmark of the disease. The study
of these abnormal proteins, in turn, has generated exten-
sive and significant knowledge not only about multiple

 
myeloma itself, but also about the nature of hereditary
deficiencies in the immune system, autoimmune dis-
eases, and the structure, biosynthesis, and genetic
control of antibodies.

The particular strand among this network of research
and discovery that we will follow is that which runs
from the first clinical descriptions and study of multiple
myeloma in the mid-19th century to the analysis of anti-
body structure in the 1950s and 1960s, an analysis
that rested on defining the nature of one of the abnor-
mal proteins of multiple myeloma patients, known as
Bence Jones protein. The elucidation of an antibody’s
structure marked the birth of molecular immunology,
an event that future historians may well judge to have
been a “revolution” in the science of immunology. One
of the first results of that revolution, as we shall see,
has been major strides in understanding how an anti-
bodys molecular structure specifies two of its functions:
to recognize a specific type of antigen, and to then
perform a particular type of defense function, termed
the antibody’s effector function.

In part because both the history of immunology and
our present knowledge of immune phenomena are so
complex, we are going to reverse our historical narrative
and begin with the end of the story: a brief account of
knowledge about the immune system, particularly the
structure and function of antibodies, as of the early
1970s. Then we will go back to the mid-19th century,
and learn why multiple myeloma has proved to be the
critical experiment of nature for unraveling the mole-
cular structure of antibodies and, in turn, for beginning
to understand how that structure specifies antibody
functions. Separate paths of inquiry about the nature
of myeloma proteins and about the nature of antibodies
were pursued until the late 1950s, and, mirroring this
historical disjunction, we will look separately at at-
tempts to answer two questions: what is Bence Jones
protein? , and what is an antibody? Finally, we will
see how these two questions converged during the
1960s, when the study of myeloma proteins entered and
profoundly affected the mainstream of immunological
research.

The Immune System's Architecture

At any given moment, there are some trillion cells
in the human body called lymphocytes, a type of white
cell which exercises the recognition, specificity, and
memory functions of the immune system. In the late

94

1960s, principally through clinical research on immuno-
deficiency diseases! immunologists learned that lym-
phocytes are composed of two cell types: B cells and T
cells. The identification of B and T cells resolved earlier
decades of often intensive debate about whether im-
munity is primarily a humoral or cellular phenomenon,
for these cells represent a dual humoral and cellular
system of immunity. In this dual system, the 7 /lympho-
cytes are responsible for the cellular immune response,
which functions against certain microorganisms and
parasites, viruses, cancer cells, and organ transplants.’
The B cells, in turn are responsible for the production
of antibodies, and thus mediate the humoral response of
the immune system. In the past few years, researchers
have found that this duality is not a complete or simple
one. There is an overlap in the responses of B and T
cells to common antigens, and the production of anti-
bodies involves not just the response of B cells to certain
antigens, but a complex cooperative response involving
T and B cells and another type of white cell, the macro-
phage.

Antibodies have been identified as large proteins,
containing about 1300 amino acids in their chains, that
are associated with the globulin class of proteins and
thus also are termed immunoglobulins. The antibody or
immunoglobulin molecules are arranged on the surface
of B cells, with any given B cell having only one type of
antibody molecule. We have noted that there are mil-
lions of possible antigens, and, correspondingly, there
are millions of different antibodies, each structured to
fit or bind to an antigen like the matching of a lock and
key.

The huge variety of antibodies have been grouped
into five classes, according to their molecular structure.
It is 1gG, the major mammalian antibody class, that we
shall refer to most often as we trace the role of multiple
myeloma research in elucidating the structure of anti-
bodies.

The first major, fundamental information revealed
by the molecular analysis of antibody structure, as we
have noted briefly, is how the antibody’s two principal
functions are determined by its structure. The anti-
body's recognition function - its ability to “identify” a
specific antigen - is governed by the shape of the antigen-
binding site in the molecule, and is unique to a given
antibody. The antibody’s effector function - its ability
to execute a given type of defensive action against an
antigen - is determined by another part of the antibody
molecule, and is common to an antibody class.
The details of antibody structure that emerged in
the late 1950s and 1960s from the union of immunology
and molecular biology have shown us that an antibody
or immunoglobulin molecule is composed of four
separate protein chains, linked together with special
types of chemical bonds. The arrangement of the four
chains give the antibody molecule as a whole the shape
of the letter Y.

An antibody’s four protein chains are composed of
two pairs: a shorter pair called the light chains, and a
longer pair called the heavy chains. The light chains
and the heavy chains, in turn, have two common struc-
tural features that determine the antibody’s recognition
and effector functions: one part of each chain is struc-
turally “constant,” while the rest of the chain is “vari-
able.”

“Constant region’’ designates that area of the heavy
or light protein chain in which the amino acid sequence
is identical, within a given immunoglobulin class. That is,
for example, the constant regions of heavy and light
chains in all 1gG antibodies have identical amino acid
sequences. Thus, molecular studies have shown that it
is the constant region of the chains which determines an
antibody’s class. And, as we have said, the antibody class
is characterized by the effector or defense function
particular to that class.

As its name implies, the variable region is that rela-
tively short area of the protein chain in which the amino
acid sequence differs from antibody to antibody. It is
this variable region that provides the antibody mole-
cule’s recognition function, or, stated another way, it
is the site of the antibody’s antigen binding capability.
The huge number of possible amino acid sequences
provided by both the heavy and light chains’ variable
regions* give each antibody its unique ability to “recog-
nize” a particular type of antigen, forming a specifically
shaped ‘lock’ or binding site that matches the antigen
“key.”

In brief summation, we know today that B lympho-
cytes have on their surfaces a particular type of large
protein molecule, called antibody or immunoglobulin.
This molecule consists of two heavy and two light
protein chains arranged in a Y-shape. Each end of the
“Y' has an antigen-binding site, in the variable regions
of the heavy and light chains. These two sites are the
same in any given antibody molecule, and they enable
the antibody to ‘“‘recognize’’ and bind with a particular
antigen. Linked to the two light chains in each antibody
are two heavy chains, and it is the long constant regions
of these chains that primarily determine an antibody’s
class and hence its effector function.

95

The knowledge of the structure of an immuno-
globulin molecule that we have summarized is a very
recent achievement in the history of immunology. It is
knowledge, as we have suggested, that has opened a
new, sophisticated, and conceptually powerful era of
molecular immunology. And, at the same time that it
has opened a new era of research, the recent detailing
of an antibody’s molecular structure is the end of a
trail of investigation that began more than a century ago,
in 1845, when Dr. Thomas Watson asked Dr. Bence
Jones, “What is it? ”’

“What is It?” Multiple Myeloma
and Bence Jones’ Proteins

The Puzzle Begins: The First Case of Multiple Myelo-
ma. Dr. Watson's query to Dr. Bence Jones concerned a
urine sample from a seriously ill patient, who died two
months after certain peculiar characteristics of his urine
had first been noticed by another physician involved in
his care, Dr. William MacIntyre. The sample, Dr. Watson
wrote in his brief note, “contains urine of very high
specific gravity. When boiled it becomes slightly opaque.
On the addition of nitric acid, it effervesces, assumes a
reddish hue, and becomes quite clear; but as it cools,
assumes the consistency and appearance which you see.
Heat relinquishes it. What is it?’ (Bence Jones 1847,
p.52).

This question, about the urinary substance that
later became known as Bence Jones protein, would
occupy the attention of clinical and basic researchers
for more than 100 years. The patient who prompted the
inquiry had the first recorded case of multiple myeloma,
which his physicians recognized as a malignant bone
disease and named ‘‘mollities ossium.”

Three astute physicians became involved in exploring
the nature of this previously unrecognized disease, and,
in a series of papers published between 1846 and 1850,
they described their findings concerning the clinical
features of the disease, the gross and microscopic post-
mortem findings, and the characteristics of the strange
urinary protein. Dr. William Macintyre, a London
physician, entered the case in October 1845, when he
was asked by Dr. Watson to see a patient whom the
latter had been treating for several months. From his
careful history and physical examination, Macintyre
discovered several important clinical features of multiple
myeloma, including severe bone pains and an unusual
protein in the urine. Although history has linked Bence
Jones’ name with the characteristic proteins of multiple
myeloma patients, it was MacIntyre who first thought to
examine the patient's urine. In so doing, he observed
 
 

that heating the sample caused an unknown protein to
precipitate at temperatures much lower than those of
other proteins, and that this protein would redissolve
as the urine’s temperature was raised, and then reprecipi-
tate as the urine cooled.

Drs. Macintyre and Watson independently sent
samples of their patients urine to another physician for
further study. They both chose Dr. Henry Bence Jones,
a physician to St. George's Hospital who was noted as
a ‘chemical pathologist.”” Bence Jones confirmed
Macintyre’s findings concerning the urinary protein,
and went on to study it in greater detail. Maclntyre’s
case report paper in 1850 dealt mainly with the clinical
features of the disease, which is doubtless why he failed
to receive historical credit for discovering the protein
(MacIntyre 1850; Clamp 1967).

The third member of this physician trio became
involved in the case after the patient's death. John
Dalrymple, a surgeon to the Royal Ophthalmic Hospital
and a member of the Microscopical Society, was asked
to do a histological study of material from the patient's
lumbar vertebrae and a rib. His paper, accompanied by
two woodcut drawings of the cells he had examined,
today would be read as a description of malignant
plasma cells (Dalrymple 1846).

The immediate cause of death listed for this first
recorded victim of multiple myeloma was “‘[kidney]
atrophy from albuminuria.” At the time, ‘““albuminuria’’
was a term used non-specifically to designate proteinuria
- the excretion of large amounts of prtein in the urine.
Dr. Maclntyre’s and Bence Jones’ recognition and anal-
ysis of their patient's abnormal urinary protein was, in
the context of their day, a significant achievement, for
the terms “protein” and ‘‘albumin’’ had just entered
the lexicon of chemistry in 1838, originally with a
meaning different from its modern usage.’

Bence Jones discussed his study of the protein that
would bear his name in 1847 and 1848 papers published
in three of England's most prestigious medical and
scientific journals: Lancet, the Proceedings of the
Royal Society, and the Philosophical Transactions of
the Royal Society.

The first paper, in Lancet, was the text of a lecture to
the Royal College of Physicians - testimony to the young
physician's eminence as a chemical pathologist. The
theme of Bence Jones’ lecture was the chemical effects
of oxygen in the human body, a topic he addressed
principally with reference to his own experiments on
the urinary products of normal subjects and patients

 

 

suffering from various diseases. Although the profes-
sional role of clinical researcher did not emerge until
the early decades of the 20th century, Bence Jones was,
in effect, working as a clinical researcher in the 1840s,
seeking to define metabolic processes in normal and
diseased human subjects.

It was in this context that Bence Jones introduced
the case he had worked on with Drs. Watson and Mac-
Intyre, stating that ‘I have found another oxide of
albumen in the urine, in a case of mollities ossium’’
(Bence Jones 1847, pp. 91-92). Bence Jones then
described the clinical symptoms and read the note from
Dr. Watson that accompanied the urine sample, before
reporting on his physical and chemical analysis of the
“enormous quantities’’ of the substance in the urine.
Reflecting the newness of protein chemistry in 1845,
Bence Jones argued that his analysis showed the sub-
stance to be an “oxide of albumen,” not an ‘‘oxide
of protein’’ (see note 5).

“It will immediately be asked,”” Bence Jones correctly
realized, ‘what is the connection between Mollities
Ossium and this state of the urine? ” “To such a ques-
tion,” he acknowledged, ‘| am as yet unable to give a
positive answer’ (Bence Jones 1847, p. 92). He did,
however, have an hypothesis to advance: chlorine,
formed by the decomposition of sodium chloride in
cells of the bones and kidney, “may have been the
cause of the solution of the earthy matter of the bone’
(i.e., of the pathological fractures of the patient's bones -
another characteristic of multiple myeloma). This
hypothesis, in turn, generated the question of “‘why do
the cells take on this peculiar action? ** Bence Jones had
no answer, but could only note that “‘on this question,
the whole of secretion and nutrition are involved’
(Bence Jones 1847, p. 92).

To Dr. Watson's query, “Waht is it? ”’, Bence Jones
thus could give only a partial answer, albeit as good a
characterization of the urinary substance’s properties
as the analytic techniques of his day permitted. He could
not, he realized, do more than guess at the exact origin
and nature of the substance, and at its relationship to
the disease, multiple myeloma. For he, together with
Drs. Watson, Macintyre, and Dalrymple, had uncovered
a medical puzzle that would intrigue scores of disease
detectives for generations to come.

A Hundred Years Later: “Much Remains to be
Learned.” As one scans the literature on multiple
myeloma that developed from the late 1840s to the
early 1950s, one initially striking impression is how

  
much attention was devoted to this relatively rare
disease by physicians and their research colleagues in
“physiological chemistry’ or biochemistry. ““Mollities
ossium,” renamed myeloma by Rustizky in 1873, be-
came a generally recognized disease entity when a Ger-
man physician alerted physicians in 1889 to the fact
that a certain constellation of symptoms usually meant
that a patient had multiple myeloma. Those symptoms,
which Dr. MacIntyre and his colleagues had first noted
in 1845, included deformity and abnormal fragility of
the bones, bone pain, cachexia (a general wasting that
occurs in chronic diseases), and the presence of Bence
Jones protein in the urine (Kahler 1889).

As clinicians encountered and defined the character-
istic signs of multiple myeloma, they discovered that the
excretion of large amounts of Bence Jones protein in the
urine was not the only protein abnormality associated
with the disease. Two other changes in protein metabo-
lism also were found: an increased level of certain abnor-
mal globulins in the serum, and the deposition of protein
in various body tissues. Of these three protein abnor-
malities, Bence Jones proteinuria received particular
attention, because, as physicians searched for its pres-
ence in other disease states, they found that it rarely
occurred except in multiple myeloma. Thus, the pres-
ence of Bence Jones protein in a patient's urine, as
Kahler emphasized, was an almost sure sign of multiple
myeloma.

Physicians became interested in Bence Jones protein,
as well as the abnormal serum protein and amyloidosis,
not only because they were characteristic indicators of
multiple myeloma. From the time it was first observed
in 1845, the etiology or cause of multiple myeloma was
a puzzle. And, as had Dr. Bence Jones, physicians hoped
that study of the characteristic changes in their patients’
protein metabolism might reveal what caused the disease.

Through the early 1950s, the study of Bence Jones
protein was pursued predominantly as a problem in
clinical medicine. Physicians and other clinically-ori-
ented researchers (mainly physiological chemists) were
attempting to solve questions about the abnormal
protein's origin and its chemical constitution primarily
in reference to questions about multiple myeloma.
Research reports and discussions of various hypotheses
about Bence Jones protein appeared as separate articles,
and as components of extensive clinical review articles
that detailed hundreds of case reports of multiple
myeloma.

The state of knowledge about multiple myeloma and
Bence Jones protein a century after the first case report
is exemplified by a 1953 clinical monograph by Snapper,
Turner, and Moscovitz, physicians at Mt. Sinai Hospital
in New York. Having extensively reviewed the literature
on multiple myeloma, and having personally dealt with
ninety-seven cases over a seven-year period, the physi-
cians wrote at the beginning of their book: “It is remark-
able that today, after more than a century of study,
much remains to be learned about the disease in general,
and the source, chemistry, and constitution of Bence
Jones protein in particular’ (Snapper et al. 1953, p. 1).

Over the course of a century, Snapper and his col-
leagues went on to note, new ideas about the disease’s
etiology gradually had developed. Most authorities no
longer regarded multiple myeloma as “‘merely’’ a tumor
derived from bone marrow. But having decided what it
was merely not, the question of what multiple myeloma
was remained a matter of several unproven hypotheses,
generated by clinical studies and, after 1935, by experi-
ments with mice in which myeloma-like tumors could be
produced. “For the time being,” Snapper and his col-
leagues had to conclude in 1953, *‘the nature and patho-
genesis of multiple myeloma remains completely un-
known. In the absence of a proven etiologic agent, our
knowledge can only be furthered by repeated and
careful clinical observation and study’’ (Snapper et al.
1953, p. 4).

The status of knowledge about Bence Jones protein-
uria in the early 1950s was much akin to that of the
etiology of multiple myeloma: many questions, a variety
of competing hypotheses, and little definitive knowledge.
To the extent permitted by physicochemical analytic
techniques as they developed over a century, investiga-
tors had pursued three major questions about this abnor-
mal urinary product: what is the metabolic origin of
Bence Jones protein, what is its chemical nature, and
what is its relationship to normal serum proteins and to
the abnormal serum proteins found in multiple myelon
patients?

Not surprisingly, ideas about the origin of Bence
Jones protein tended to be linked with the development
of myeloma itself. Thus, many favored a hypothesis
put forward in the 1930s, that Bence Jones protein
is formed by the malignant myeloma cells in the bone
marrow (Magnus-Levy 1938). One extension of this idea,
cited often in the literature after it was proposed by
Dent and Rose in 1949, also sought to account for the

 
cause of myeloma itself. Dent and Rose reported, on the
basis of their analysis of one patient's urine, that Bence
Jones protein was one of a small group of proteins,
including the tobacco mosaic virus, that lacked the
amino acid methionine in its composition. This finding,
in light of the current knowledge about the structure
and function of viruses, suggested that multiple mye-
loma “is due to invasion of the body by a virus which
lives and multiplies in the plasma cells of the bone
marrow. . .lt is further suggested that the Bence Jones
protein, when combined with nucleic acid in the plasma
cells, is the virus itself” (Dent and Rose 1949, pp. 616-
617).

Another view was that Bence Jones protein was more
indirectly the product of the bone marrow’s malignant
myeloma cells. In part reasoning from the fact that the
protein had been found to have a relatively low molecu-
lar weight, Rundles and his colleagues cautiously pro-
posed that “the serum components. . .are produced in
all likelihood by the abnormal plasma cells. . .Bence
Jones proteins could possibly be derived from the
abnormal serum constituents, since the latter have a
molecular weight about three to six times as great, if
the latter were to disintegrate or be split into protein
moities filterable through the glomeruli [of the kid-
neys] ” (Rundles, Cooper and Willett, p. 1125).

Yet another school of thought held that Bence Jones
protein is not an abnormal product somehow triggered
by myeloma. Rather, as Meyler suggested, Bence Jones
protein is produced by normal bone marrow, but in
quantities too small to be detected in a normal person's
urine or blood serum. When myeloma develops, how-
ever, the protein’s production increases so greatly that
it is excreted in readily detectable amounts in the
urine (Meyler 1936).

These and other ideas about the source of Bence
Jones protein were, by and large, as speculative as Dr.
Bence Jones’ original idea. Lack of knowledge about
the etiology of myeloma itself, the fact that a given
investigator usually had only one or at best a few pa-
tients’ samples to study, and technical difficulties in
isolating and analyzing Bence Jones protein, all contrib-
uted to the high degree of uncertainty about where this
urinary protein came from. These same factors also
bore upon the decades of conflicting ideas and data
about the protein's chemical nature. Up to this point
in our narrative we have used the singular, Bence Jones
protein, to reflect the historical fact that for many
decades it was generally regarded and discussed as a

98

homogeneous substance, identical in all multiple mye-
loma patients. Two French investigators, Ville and
Derrieu, had suggested in 1907 that the protein might
not be the same in all cases, but the early literature
generally cited a 1911 paper by Hopkins and Savoy.
The latter, after analyzing the amino acid composition
of Bence Jones protein obtained from two patients,
concluded that the chemical composition was identical
(Hopkins and Savoy 1911).

The plural term, Bence Jones proteins, reflecting
knowledge that the substance was not chemically
identical in all patients, did not enter the literature until
the 1920s, and one finds even today that the singular
term continues to be used. Given the ultimate signifi-
cance of Bence Jones proteins vis-a-vis our understanding
of antibody structure, it is interesting that attempts to
identify and characterize the abnormal proteins of
myeloma patients relied heavily on immunologic meth-
ods. But, and this is an important historical ‘“but,’’
these immunological methods were used for decades
simply as useful analytic techniques, quite independent
of the work on antibodies by immunologists and bio-
chemists that eventually would involve Bence Jones
proteins.

By the early 1900s, knowledge of antigenic reactions
gained by the medical bacteriologists who pioneered the
early development of immunology had begun to indicate
that proteins have individual antigenic specificity (see
Bulloch 1938, Lechevalier and Solotorovsky 1974).
Thus, immunological reactions were recognized by
physiologists and chemists as a useful way of detecting
differences in proteins that, by other criteria, appeared
alike. Two chronologically scattered reports on the
study of Bence Jones proteins by immunologic methods
appeared in 1911 and 1921; both showed, contrary to
earlier studies, that the protein was not the same as
normal serum protein (Massini 1911; Hektoen 1921).

Then, in 1922, these reports were confirmed and
extended by Bayne-Jones and Wilson from Johns Hop-
kins, who used immunologic tests to study normal
serum proteins and twelve samples of Bence Jones
proteins obtained from five patients. They found, first,
that “the Bence Jones proteins are immunologically
different from the proteins of normal human serum,”
and these results, they noted, supported a newly emerg-
ing major concept in protein research - ‘‘that the speci-
ficity of proteins is not dependent upon their biological
origin, but due to their chemical composition’ (Bayne-
Jones and Wilson 1922a, p. 43). Bayne-Jones and

 
Wilson's work also challenged the “tendency to assume
that all preparations of Bence-Jones protein are identical
in structure and composition.” For they had found
that, immunologically, their preparations could be
categorized into ‘‘two and possibly three groups.”
Thus, they concluded, Bence Jones “protein” actually
is a group of similar but not identical protein substances
(Bayne-Jones and Wilson 1922b).

Bayne-Jones’ and Wilson's work, as well as earlier
studies of the constitution and characteristics of Bence-
Jones proteins, was subject to a major criticism. Most
preparations of the protein were impure, containing
other urinary or serum substances, and thus the results
of a given experiment could not unequivocally be
attributed to Bence Jones protein. By the 1940s, how-
ever, researchers were able to obtain crystallized protein
extracts more readily and reliably. Repeating earlier
immunological studies with these purer samples, investi-
gators confirmed the existence of two immunologically
distinct groups of Bence Jones proteins, and found,
further, that a given patient may excrete both types
(Hektoen and Welker 1940).

In the 1940s, researchers also began to use other
new techniques such as ultracentrifugation and electro-
phoresis in addition to immunological tests, that per-
mitted more precise qualitative and quantitative charac-
terizations of the metabolic abnormalities in multiple
myeloma. By using a “broad and flexible analytic
approach,” as Moore and his colleagues noted in 1943,
investigators hoped to sort out ‘‘the multiplicity of
Bence Jones proteins and. . .their correspondingly varied
properties. . .[and] the varied serum protein patterns of
patients with Bence Jones proteinuria” (Moore, Kabat
and Gutman 1943, p. 74). By the early 1950s, the use of
a combination of techniques had produced a mass of
detailed information about the properties of Bence
Jones proteins and the abnormal serum proteins of
myeloma patients. But the findings of different research-
ers did not always accord, and so the exact nature of
and relationship between the various protein abnormali-
ties associated with myeloma remained “still a matter
for conjecture’’ (Snapper et al. 1953, p. 58).

First Answers: Biochemical and Immunologic Studies
in the 1950s. When Snapper and his colleagues observed
in 1953 that ‘‘the exact nature of Bence Jones protein
has never been determined,’ a series of studies had
begun that would yield the first tentative answers to
the question originally posed by Dr. Watson in 1845.
These investigations of Bence Jones and other myeloma

proteins in the 1950s fall into two major groups in
terms of methods. First, as represented by the work of
Frank W. Putnam and his associates at the University
of Chicago, new knowledge about the structure and
origin of Bence Jones proteins began to emerge from
quantitative and qualitative biochemical analyses of
multiple myeloma proteins. Secondly, investigators
continued to examine the immunological relationships
among the various abnormal proteins found in myeloma
patients, and in so doing also uncovered new informa-

"tion about the nature of Bence Jones proteins. Repre-

sentative of this work in the 1950s was the research by
Korngold and Lipari at New York's Sloan Kettering
Institute for Cancer Research and Cornell Medical
College's Department of Biochemistry, and that by
Slater and his associates at the Hospital of the Rocke-
feller Institute for Medical Research.

In examining the work on myeloma proteins in the
1950s, one finds a significant shift in the objectives of
the researches. Through the early 1950s the abnormal
proteins of multiple myeloma had been investigated
primarily - although not exclusively - in relation to the
light they might shed on the disease itself. Some investi-
gators, particularly those like F. G. Hopkins who were
based in university laboratories rather than hospitals,
also studied Bence Jones protein because ‘‘a proper
understanding of the disturbances involved could hardly
fail to throw light on normal protein metabolism"
(Hopkins and Savoy 1911, p. 190). But, in the main, the
literature on abnormal myeloma proteins through the
early 1950s indicates that these proteins were objects
of clinical research, studied in reference to questions
about multiple myeloma.

From the early 1950s on, however, one finds an
increasing focus of interest in the myeloma proteins as
“experiments of nature,” as abnormal substances whose
study might yield knowledge about the normal synthesis
and structure of proteins in general, and about the
globulin class of proteins in particular. In the remainder
of this chapter, the trails of investigation that we will
follow are those that led from Bence Jones proteins to
the birth of molecular immunology. Once again, of
course, this has not been the exclusive focus of research
since the 1950s, for, as in earlier decades, the abnormal
proteins of multiple myeloma have continued to be
studied in reference to this and other diseases. And,
as one looks at sources of support since the early 1950s
for the increasingly basic lines of research that utilized
Bence Jones proteins, one finds that it has come princi-

 
pally from government and private sources that recog-
nize the joint medical and basic science import of the
work. Thus, for example, Putnam's work in the 1950s
was supported in part by the National Cancer Institute
(NCI) and a private University of Chicago Fund, Korn-
gold’s researches by the Atomic Energy Commission and
the NCI, and Slater's work by the Rockefeller Institute
for Medical Research. Finally, in noting a shift of
emphasis in the study of Bence Jones protein in the
early 1950s, it is worth re-emphasizing that the work
hinged on the existence of patients who, whatever the
objectives of the various researchers, served as research
subjects because they were afflicted with a critical
experiment of nature.®

One of the major figures in the recent intertwined
history of research on Bence Jones proteins and the
structure of antibodies is biochemist Frank Putnam.
The first of his many papers on multiple myeloma pro-
teins appeared in 1953 when Putnam was at the Univer-
sity of Chicago. In his first foray into myeloma proteins,
Putnam used sera from twenty-five patients to do
quantitative physicochemical studies of the abnormal
serum globulins, seeking, as had others before him, to
determine their relationship to normal globulins (Put-
nam and Udin 1953). He had also launched studies of
Bence Jones proteins, seeking to define their chemical
structure and their metabolic origin. These serum and
urinary proteins, Putnam explained, were of great inter-
est to him as a protein chemist because ‘‘the profuse
synthesis and diverse nature of the proteins elaborated
in multiple myeloma constitute the most profound
alteration in protein metabolism in any disease. It may
be hoped that the biochemical study of this striking
phenomenon may have import in the analysis of the
mechanism of protein synthesis’’ (Putnam and Stelos
1953, p. 357).

In his first paper on Bence Jones proteins, Putnam
dealt with the still-debated question of whether they
were chemically identical substances. His comparative
physical and chemical analysis of Bence Jones protein
from eighteen myeloma patients, Putnam reported,
“has shown that in no instance are the proteins identical
in physicochemical properties” (Putnam and Stelos
1963, p. 356; see also Putnam and Miyake 1954).
Physicochemical evidence for the conclusion that
different patients excrete different Bence Jones proteins,
Putnam noted, had been repeatedly supported by
immunological studies showing that ‘there are at least

100

two antigenically specific groups of these proteins.”
But just what the diverse substances are was still a
puzzle, one that Putnam sought to solve by studying
their metabolic origin.

To tackle the question of the origin of Bence Jones
proteins, Putnam and Sarah Hardy conducted isotopic
studies on two patients, to trace the rate of synthesis
and possible chemical precursor relationships of both
myeloma globulins and Bence Jones proteins (Hardy
and Putnam 1953; Putnam and Hardy 1955; Hardy
and Putnam 1955). Several important findings, bearing
on many debated questions about the nature of and
relationship between serum and urinary proteins, emerged
from these technically complex studies.

Putnam and Hardy found, first, that the serum
globulin and Bence Jones proteins appeared to be
synthesized independently in the patient's body. This
and other data overturned a long-held hypothesis about
the origin of Bence Jones proteins: that they were
breakdown or degradative products of normal tissue
proteins or of serum proteins. Rather, Putnam and
Hardy found Bence Jones proteins to be synthesized
"de novo’ by the myeloma patient, and to be derived
directly from the body's pool of metabolic nitrogen
rather than from any tissue or plasma protein precursor.

Up to this point in their researches, Putnam and his
colleagues had established two important ‘nots’ about
Bence Jones proteins. They are not physicochemically
identical, and they are not formed as breakdown pro-
ducts of protein metabolism. What the proteins are - in
terms of their structure and the site of their synthesis -
remained uncertain; but the boundaries of the puzzle
had been greatly clarified by these “nots.”

We will resume our account of Putnam’s work on
Bence Jones proteins’ structure and origin in a later
section, when we move to the studies in the 1960s that
elucidated antibody structure. Clues to this latter line
of research, that would link together the efforts to
determine the nature of Bence Jones proteins and
the attempts of immunologists to decipher the structure
of antibodies, emerged in the 1950s, through further
immunological studies of myeloma proteins. The work
of two research groups, in particular, pointed to the
identification of Bence Jones proteins, and how that
identification would lead to the molecular analysis of
antibody structure.

At the Rockefeller Institute for Medical Research, a
group of investigators in 1950 were seeking to define the

 
immunological properties of normal human gamma
globulin (protein antibodies), which had just been
successfully purified. Their work, they found, was
hampered because the various gamma globulin fractions
were not single proteins. To overcome this problem,
they seized upon ‘‘the special readily purified” serum
proteins found in ‘‘tremendous quantity’’ in myeloma
patients, hoping that study of these abnormal serum
proteins would help to “clarify the relationship between
the fractions of (normal) gamma globulin’ (Kunkel,
Slater, and Good 1951, p. 190).

The physicians who undertook this project in 1950
included Dr. H. G. Kunkel, Dr. A. J. Slater, and a young
fellow at the Institute, Dr. Robert A. Good.” After
demonstrating an immunological relationship between
myeloma serum globulin and fractions of normal gamma
globulin, Kunkel and Slater went on to study the im-
munological relationships between the myeloma serum
globulins from a series of twenty-one patients. Three
British investigators had shown in 1950 that myeloma
serum globulin has two immunologically distinct com-
ponents, gamm and beta (Wuhrmann, Wunderly, and
Hassig 1950). As had this and previous studies, including
Putnam’s, the Rockefeller group's work indicated that
every one of the myeloma proteins was different and
individually specific to a given patient. But there also
were commonalities, as the British study had found: the
myeloma gamma globulin proteins were related immuno-
logically to each other and to normal gamma globulin;
the myeloma beta globulins similarly were interrelated,
but were mostly distinct from the gamma globulins.

These findings on the immunological relationships
among normal and myeloma globulins, Slater and
Kunkel realized, had important implications for under-
standing the origin of myeloma proteins.

Insufficient knowledge of the properties of normal
serum proteins had made it difficult to determine
conclusively whether multiple myeloma proteins
are truly abnormal entities or simply represent a
great elevation of a single one of the many normal
globulin components. In general the data obtained
in the present study favor the hypothesis that
these proteins are not normal but related to nor-
mal constituents.

It is tempting to consider the myeloma proteins as
intermediates in the synthesis of y-globulin and
antibodies with the more closely related myeloma

101

 

proteins having most of the determinant groups of
v-globulin. However, definite evidence on this
point is lacking. (Slater, Ward, and Kunkel 1955,
p. 106)

During the same time period, a more specific focus
on the immunologic relationships between Bence Jones
protein and normal and myeloma serum proteins was
being pursued at Sloan Kettering Institute by Korngold
and Lipari .® Citing both the Rockerfeller group's work
and Putnam’s researches, and thanking Putnam for his
“valuable suggestions and criticisms,’”” Korngold and
Lipari reported on their own immunological studies
in two papers in Cancer during 1956. In their first
paper, on an antigenic analysis of myeloma serum
globulins, Korngold and Lipari reported that their data
were ‘‘compatible with the theory that MM (Multiple
Myeloma) globulins are altered gamma-globulins (Korn-
gold and Lipari 1956a, p. 191).

Then, in their second paper, Korngold and Lipari
addressed the relationship between Bence Jones (BJ)
proteins and serum proteins (globulins). Experiments
from the 1920s on, they observed, “have created the
impression that BJ proteins are antigenetically distinct
and unrelated to eith MM globulin or normal gamma-
globulin.” But newer techniques had “made a properly
controlled study of such antigenic relationships pos-
sible.” In doing such a controlled antigenic study,
Korngold and Lipari demonstrated, in contrast to
previously accepted views, that Bence Jones proteins
“are related to both normal gamma-globulins and the
MM globulins’’ (Korngold and Lipari 1956b, p. 268).
They also found, as had many prior invesitgators, that
there are antigenic differences among Bence Jones
proteins. And, going a step further, they showed that
the urine of a given myeloma patient contains two
major antigenic types of Bence Jones proteins (subse-
quently designated as K and L).

As had other investigators for many decades, Korn-
gold and Lipari brought their findings to bear on the
question of the origin of Bence Jones proteins. “The
immunologic data presented here,” they wrote in 1956,

show that BJ protein is antigenically related to
norma gamma-globulin and the patient's abnormal
MM globulin. Since BJ protein contains deter-
minants present in MM globulin but not in normal
gamma-globulin, it must be assumed that it is more
closely related to the former. . .In the light of the

 
 

foregoing considerations, it may be speculated
that BJ proteins are produced by cells that are no
longer capable of synthesizing the complete MM
globulin. The incompletely synthesized proteins,
which are smaller and more deficient in antigenic
groupings than the serum proteins, are excreted
into the urine as BJ proteins. (Korngold and Lipari
1956b, p. 217)

In this “speculation,” as the next decade of research
would show, lay both the answer to Dr. Watson's ques-
tion about Bence Jones protein, and the means for
immunologists to uncover the structure of the antibody
molecule.

What is it?: Ideas About Antibody and Immunity

To appreciate the impact that the identification and
structural analysis of Bence Jones proteins had upon
immunology in the 1960s, we need to look briefly at
another “What is it? "’ question, one asked quite inde-
pendently of work on myeloma proteins, by those who
sought to determine the nature of antibodies and how
they interacted with antigens. This path of inquiry,
long and complex, can be dealt with here only briefly
and selectively, to suggest the nature of theories about
antibodies through the 1950s and thus set the stage for
seeing how the study of Bence Jones proteins entered
into immunology.

The science of immunology began to develop in the
last decades of the 19th century as one of the major
yields of the new field of bacteriology. “The whole
initial concept of immunity,” as Burnet has pointed
out, “was in relation to infectious disease in man or his
domestic animals. . .once [Pasteur] had shown the
potentiality of immunization with attenuated pathogens
(1880) the central objectives of immunological research
were defined for the next sixty or seventy years. Im-
munology was one of the practically important aspects
of medical bacteriology and almost all those concerned
with its advance were medically trained’ (Burnet 1969,
p. 5).

By the late 1880s, building on Pasteur’s epochal
achievements between 1880-1885 with attenuated
vaccines against diseases such as fowl cholera, anthrax,
and rabies, the new field of immunology began develop-
ing in two major, often intersecting directions (Pasteur
1880a,b, 1884, 1885; Pasteur, Chamberland, Roux
1885). The enormous practical implications of vaccines,
first, generated continuing efforts to extend the range

102

of diseases for which prophylactic innoculations could
be developed, and to find new ways of preparing such
vaccines (see Parish 1965). Secondly, medical bacteriolo-
gists began attempting to explain the mechanisms or
processes responsible for immunity. The identification
of specific pathogenic bacteria focused attention on the
question of why animals, including man, are normally
resistant to most bacteria. At the same time, the devel-
opment of vaccines framed questions about how im-
munity is produced and about the process of recovery
from an infectious disease.

From the mid-1880s through the early years of the
20th century, much of the effort to explain the nature
of immunity revolved around what were seen as two
opposing explanatory models. The cellular theory held
that immunity depends upon the ability of certain white
cells in the body, phagocytes, to engulf infective mate-
rials and destroy them by a process of intracellular
digestion (Metchnikoff 1888, 1901, 1908). The other
major contender was the humoral theory, which pro-
posed that certain substances or properties in the body
fluids, principally the blood, were responsible for
immunity (Nuttall 1888; Buchner 1890, 1900). The
debate that flourished between proponents of cellular
and humoral theories of immunity was one of the
classic controversies that dot the history of science,
generating fruitful research and ideas as well as polemical
attacks and counterattacks. As often happens, this
controversy abated when researchers recognized that
their work pointed to the involvement of both humoral
and cellular factors in immunity, a view that eventually
would be confirmed in the 1960s with the discovery of
the dual system of immunity residing in the T and B
lymphocytes.

In the midst of the cellular vs. humoral theory
debate, a major landmark in the history of immunology
was established on December 4, 1890, when the discov-
ery of antitoxin was announced by Emil von Behring
and Shibasaburo Kitasato, researchers in Robert Koch's
Berlin laboratory. Their discovery posed a major chal-
lenge both to the cellular theory and to relatively simple
humoral explanations of immunity, opened up the
field of serology, and, most importantly for our pur-
poses, focused attention on what later would be termed
the antigen-antibody relationship (von Behring and
Kitasato 1890, transl. in Brock 1962; von Behring 1901).

Von Behring and Kitasato’s experiments provided
the first evidence that substances which are able to
neutralize foreign materials are formed in blood serum
in response to infection. And, as they showed in the case
of tetanus toxin, these antitoxic substances are highly
specific. In the wake of this discovery, researchers soon
demonstrated that animals can produce antitoxins
against a wide range of poisonous substances. The
extensive experiments and theories of Paul Ehrlich
proved particularly important, for his work both broad-
ened the scope of immunology beyond its early focus
on infectious diseases, and began to direct the attention
of immunologists to what they later would call anti-
bodies (Ehrlich 1891, 1897, 1900, 1908; Marquardt
1951).

By the turn of the century, a series of crucial ques-
tions had been framed about the nature of antibodies
and antigens and how they interact, questions that only
have begun to be answered in fine detail since the 1960s.
The antitoxin experiments quickly revealed one of the
most striking properties of antibodies, their specificity,
and in turn posed the question of the source or mecha-
nism of this specificity. Initial ideas centered on the
toxin as the source of specificity, but by 1900 a variety
of experiments had shown that antibodies were some-
thing other than modified toxins, some sort of special
substances in the body that acted in specific response
to the presence of an antigen.

One of the first major general theories of immunity
that attempted to account for the origin and specificity
of antibodies was the ‘‘side chain’’ theory developed by
Paul Ehrlich in 1897. Ehrlich’s theory, a blend of late
19th century biological and chemical fact and fancy,
proposed that certain cells in the body have special
preformed side-chains or groups of atoms that perfectly
fit a grouping of atoms in a toxin - like a match between
a lock and key. Once a side chain or antitoxin has
become locked into a toxin, and its parent cell thus
made inactive, Ehrlich supposed that the body began to
manufacture more of the side chains, thus accounting
for antitoxin production (Ehrlich 1900).

Ehrlich’s theory generated vast amounts of research
and discussion by both its supporters and critics. A
major challenge to his theory, and another significant
broadening of immunology’s scope of inquiry, was set
into motion in 1898 when Pasteur’'s protegé, Jules
Bordet, demonstrated the immune lysis (destruction) of
red blood cells (Bordet 1898, 1899, 1903). Bordet's
work triggered an increasing interest in the immunolo-
gical behavior of both cells and body fluids. Then, Karl
Landsteiner showed that any molecule, either natural
or artificial, could stimulate an immune response under

103

certain conditions, a finding that argued against the
validity of Ehrlich’s theory (Landsteiner 1930, 1946).
For it was hard to conceive, as the side-chain theory
demanded, that the body had an infinite number of
preformed side-chains or receptors on its cells, capable
of fitting specifically to a structurally infinite variety
of antigens.

Rather, Landsteiner’s work with artificial antigens
seemed to indicate that antigens govern the specificity
of antibodies by somehow directing or “instructing”
the cell's activities. Instructive theories of antibody
formation gained in sophistication and status in the
1940s with the entry of Linus Pauling into immunology,
for his work began an “effective association of im-
munology with the developing principles of biochem-
istry (Burnet 1969, p. 5). Stimulated by conversations
with Karl Landsteiner, Pauling had begun to work on
the molecular bases of serological reactions in the
mid-1930s. From this work, in turn, he developed, in as
precise form as the time permitted, what is now recog-
nized as the classical instructive theory of antibody
formation (Pauling 1940).

Between 1940 and the mid-1950s, modifications of
Pauling’s instructive theory were proposed by several
researchers, consonant with new methods and knowl-
edge in protein chemistry and immunology (see Burnet
1963). At the same time, it also became evident that a
number of important immunological phenomena could
not be explained by instructive theories. In particular,
these theories could not account for the persistence of
modified immunological reactivity, or for the fact that
antibodies usually are not produced against chemical
configurations normally present in the body (the phe-
nomenon of immunological ‘‘recognition’’) (Burnet
and Fenner 1949). Such considerations led to the
development of various ‘‘selective’’ theories of antibody
formation, a development linked most closely with the
work of Australian virologist and immunologist F.
MacFarlane Burnet.

Beginning with his 1941 book, The Production of
Antibodies, Burnet had carefully studied and critiqued
instructive theories, and sought to interpret antibody
formation primarily in biological rather than in chemical
terms.’ But, as Burnet himself recognized, the first
major alternative to the generally accepted instructive
theory came in 1955, when Danish immunologist Niels
Jerne proposed a ‘‘natural selection theory’’ (Jerne
1955, 1967). Jerne's theory served to explain why the
body does not make antibodies against its own constit-

 
 

  

uents; why, in Burnet’s work, it recognizes ‘self’ as
opposed to ‘not self.” But there were explanatory
deficiencies in Jerne’s theory which were met in 1957 by
new forms of a selection theory, developed indepen-
dently by David Talmage at the University of Colorado
and by Burnet (Talmage 1957, Burnet 1957).

Both Talmage and Burnet recognized the variety of
globulins that can be present in the blood, and felt that
a satisfactory theory of antibody production should
assume that the antibody-replicating elements were
cells (like various globulin cells or their precursors),
rather than, as in Jerne's view, extracellular protein
able to replicate only if incorporated into a particular
cell type like the phagocyte. Burnet developed this
conviction in terms of a “clonal” selection theory (the
word “clone” designates a group of cells that originate
from the same parent cell). “In its simplest form,”
Burnet has explained:

the “clonal selection’ theory postulates that, in
the course of embryonic differentiation, a very
large number of clones of mesenchymal cells arise,
each carrying a specific immunological potentiality
to react with a single antigenic determinant.
Depending on various circumstances, the reaction
following contact with antigen may be manifested
in one of three different forms: (a) the cell may be
damaged so that its capacity to multiply is lost, or
it is actually destroyed; (b) it may be stimulated
to proliferate; or (c) it may undergo conversion to
plasma cell character and produce and liberate
antibody. Antibody production follows the
normal rules of protein synthesis, the information
needed for its specificity being stored in the cell
genome. (Burnet 1963, pp. 91-92)

Through the late 1950s and into the 1960s, Jerne,
Talmage, Burnet and other proponents of a selective
theory of antibody formation and action argued length-
ily and persuasively for the logical correctness of their
views. But, as they knew, instructive theories had long
held sway, and at the time there was no direct experi-
mental evidence to confirm one or the other school of
thought. By the early 1970s, however, new lines of
evidence pointed to the essential validity of selective
theories and, in the words of Gerald Edelman, “the
fundamental idea of these theories is now the central
dogma of modern immunology: molecular recognition
of antigens occurs by selection among clones of cells
already committed to producing the appropriate anti-

 

bodies, each of different specificity’ (Edelman 1973,
p. 830).

Looming large among the evidence that established
clonal selection as the central dogma of modern im-
munology was the molecular analysis of antibody
structure. And, as we resume our chronicle of Dr. Bence
Jones’ strange protein, we will learn how it served in the
1960s as the crucial experiment of nature for that
analysis.

Bence Jones Proteins, Light Chains,
and the Structure of Antibodies

By the late 1950s, the study of myeloma proteins had
generated a number of provocative clues to the identity
of Bence Jones proteins. These myeloma proteins now
were known to be antigenically related to both normal
and myeloma immunoglobulins, and hence it seemed
reasonable to speculate that BJ proteins might represent
intermediary or incompletely synthesized immuno-
globulins.

During this same period, in the late 1950s, immunolo-
gists and molecular biologists began an intensive attack
on the structure of antibodies. As we saw in the preced-
ing section, there was a substantial body of information
and theories about the functions and origins of these
proteins, but little was known about their detailed chem-
ical structure. Determining the structure of antibodies,
researchers knew, should provide understanding of their
unique specificity for antigens, and perhaps a basis for
choosing between instructive and selective theories of
antibody production. But researchers had been con-
founded by the experimental problems created by two
aspects of antibodies: they are very large proteins (with
a molecular weight of 150,000 or greater), and they are
very heterogeneous chemically (a problem, too, for
those who had been working on Bence Jones proteins).

The ultimately successful quest to define the mole-
cular structure of an antibody was launched during
1958, in researches centered at the Rockefeller Institute
in New York, and in the Department of Immunology
at St. Mary's Hospital Medical School in London. The
leaders of the two research teams were physician-im-
munologist Gerald Edelman and biochemist-immunolo-
gist Rodney Porter, who in 1972 would be honored with
the Nobel Prize in Physiology or Medicine for their
structural studies of immunoglobulines.

Rodney Porter, who had trained as a biochemist
under Frederick Sanger, developed a method of breaking
an immunoglobulin molecule into analyzable fragments

  
by using protein-dissolving enzymes. One of his major
findings from this work, which occupied years of effort,
was that the immunoglobulin G (IgG) molecule con-
tained three globular fragments: an ‘“‘Fc” fragment
common to all molecules, and two identical “Fab”
fragments, each of which carried a specific antigen-bind-
ing site (Porter 1959, 1973).

In New York, Edelman developed another approach
to cleaving 1gG molecules that involved breaking their
disulfide bonds and then exposing the molecule to
dissociating solvents. By these methods, Edelman found
that the IgG molecule was not, as had been thought,
composed of a single polypeptide chain, but rather was
composed of several discrete chains linked by disulfide
bonds. This first phase of his research also indicated
that the IgG molecule had two kinds of polypeptide
chains, later named heavy and light chains, and that
these chains were not the same as the fragments Porter
had obtained with his enzyme cleavage method (Edle-
man 1959; Edelman and Poulik 1961). Understanding
the gross structure of antibodies, then, would involve
determining the relationship between the polypeptide
chains isolated by Edelman’s methods and the fragments
found by Porter.

The second major obstacle to a structural analysis,
however, still confronted researchers in 1960: the
enormous chemical diversity of antibodies. As Edelman
recalled in his Nobel address, this chemical diversity
posed ‘‘two challenging questions.’

First, did the observed heterogeneity of antibodies
reside only in the conformation of their polypep-
tide chains, as was then widely assumed, or did
this heterogeneity reflect differences in the pri-
mary structures of these chains, as required
implicitly by the clonal selection theory? Second,
if the heterogeneity did imply a large population
of molecules with different primary structures,
how could one obtain the homogeneous material
needed for carrying out a detailed analysis?
(Edelman 1973, p. 831)

An ‘‘accident of nature rather than direct physico-
chemical assault” proved to be the means by which
Edelman and his colleagues were able to deal simultane-
ously with both of these challenges. Drawing upon the
prior work by Putnam’s group and by Slater and Kunkel
at the Rockefeller, Edelman realized that Bence Jones
proteins would provide him with a readily available,

105

 

relatively homogeneous and low molecular weight sub-
stance, known to be antigenically related to immuno-
globins.

By 1961, Edelman had begun to formulate “a unify-
ing hypothesis. . .for the structure of proteins in the
[immunoglobulin] family.” 1gG molecules, he and
Poulik stated, ‘‘appear to consist of several polypeptide
chains linked by disulfide bonds,” and bivalent anti-
bodies ‘may contain two chains that are similar or
identical in structure.” Thus, the heterogeneity and
antigenic specificity of antibodies “may arise from
various combinations of different chains as well as from
differences in the sequence of amino acids within each
type of chain’’ (Edelman and Poulik 1961, p. 880).

The discovery that immunoglobulin molecules consist
of several polypeptide units, Edelman recognized, also
had ‘‘a possible bearing upon the pathenogenesis of
diseases of gammaglobulin production.” “A primary
defect in. . .multiple myeloma,’’ he suggested, ‘may be
a failure of specificity and control in production and
linkage of various subunits to form larger molecules.”
Thus, he and Poulik were able to propose a structural
basis for previous speculations that Bence Jones proteins
were incompletely synthesized myeloma globulins.
“Bence Jones proteins may be polypeptide chains that
have not been incorporated into the myeloma globulins
because of a failure in the linkage process’ (Edelman
and Poulik 1961, p. 881; see also Poulik and Edelman
1961).

Edelman’s hypothesis about the nature of Bence
Jones proteins was confirmed “‘one exciting afternoon”
when he and a graduate student, Joseph Gally, “heated
solutions of light chains isolated from our own serum
immunoglobulins in the classical test for Bence Jones
proteinuria’’: the test used by Dr. Watson in 1845, that
had generated a century of efforts to identify Bence
Jones proteins. Dr. Watson's question, “What is it? ”,
at last was answered. Edelman and Gally, aware of the
history underlying their own work, noted that “Dr.
Jones concluded that it was the ‘hydrated deutoxide of
albumin.” [Our] studies would supply the question with
another qualified answer: Bence Jones proteins appear
to be polypeptide chains of the L [light chain] type that
have not been incorporated into myeloma proteins’
(Edelman and Gally 1962, p. 225). What the Rockefeller
investigators had observed was that their serum immuno-
globulin light chains ‘behaved as Bence Jones proteins,
the solution first becoming turbid, then clearing upon

 
further heatings. A comparison of light chains of mye-
loma proteins with Bence Jones proteins. . .confirmed
the hypothesis (Edelman 1973, p. 831; Edelman and
Gally 1962, 1968; Mannik and Kunkel 1962).

The Rockefeller group’s experiments, by 1961, had
three major implications for a molecular structure-
activity analysis of antibodies. First, “because different
Bence Jones proteins had different amino acid composi-
tions [as determined by Putnam and others in the
1950s], it was clear that immunoglobulins must vary in
their primary structures.” Second, this deduction in
turn “lent strong support to selective theories of anti-
body formation.” Third, because Bence Jones proteins
now were known to be identical or analogous to light
chains, with a relatively low molecular weight, it had
become possible to begin “‘a direct analysis of the
primary structure of an immunoglobulin moelcule’
(Edelman 1973, p. 832).'°

The first laborious analyses of the amino acid se-
quences in Bence Jones proteins were undertaken by
Hilschmann and Craig at the Rockefeller and by Frank
Putnam, then heading a laboratory group at the Univer-
sity of Florida College of Medicine. By spring 1965,
partial sequence analyses of several different Bence
Jones proteins had revealed another key feature of anti-
body structure: the structural diversity between light
chains was limited to what became known as the variable
region of the chain (Hilschmann and Craig 1965; Titani
and Putnam 1965; Titani, Whitley et al. 1965; Putnam
and Easley 1965)."!

Through the mid-1960s structural analysis was
focused on the antibody molecule’s light chain, because
of the natural experiment afforded by Bence Jones
proteins. Less work was being done on the other type of
polypeptide chain identified by Edelmann'’s experi-
ments, the heavy or H chain. But by 1964, even in the
absence of much detailed knowledge, comparisons
between heavy and light chain structure had shed light
on another reason for the diversity of antibodies: the
existence of antibody classes. Comparisons of chain
structure in the first three classes to be identified showed
that classes have similar kinds of light chains, and that it
is structural differences in their heavy chains which give
them their distinctive class characteristics or effector
functions (Bull. WHO 1964).

From the mid-1960s on, the analysis of both the
heavy and light chains of antibodies moved forward
at an accelerating pace, generating an increasingly more

106

detailed picture of an antibody molecule’s structure
and new glimpses into how that structure governs
an antibody’s functions. In 1962, Rodney Porter and his
colleagues in London had begun to link their analysis
of the molecule’s Fc and Fab fragments with the Edel-
man group's study of polypeptide chains. From this
work Porter hazarded what proved to be a brilliant
guess: the IgG molecule is composed of two large
(heavy) polypeptide chains and two smaller (light)
chains, making in total a four polypeptide chain struc-
ture (Fleischman, Pain, Porter 1962; Fleischman, Porter,
and Press 1963).

Aided by this new understanding of the relationship
between chain structure and Porter's enzyme fragments,
plus the growing knowledge about the structure of
Bence Jones proteins, Edelman and Gally in 1964
developed a topological model of the IgG molecule
(Edelman and Gally 1964). Then, in 1965, Edelman
judged that it was feasible to begin working out the
complete molecular structure of an immunoglobulin
molecule, and set to work on a sample of human mye-
loma IgG.

While Edelman’s group was laboring in New York,
Frank Putnam and his associates, now at the University
of Indiana, were pursuing their painstaking mapping of
the amino acid sequences in type K and L Bence Jones
proteins (the two major antigenic types identified by
Korngold and Lipari in 1955). In 1966, Putnam's
group published a ‘‘tentatively’” complete amino acid
sequence for type K, and in 1967 reported a complete
sequence analysis for type L Bence Jones protein (Put-
nam, Titani, Whitley 1966; Wikler, Titani et al. 1967;
Putnam 1969). Thus, for the first time, researchers had
accomplished the task of determining the structure of a
Bence Jones protein, and hence of a light chain in the
antibody molecule.!?

Sowving the complete primary structure of an anti-
body molecule, the task undertaken with myeloma 1gG
by Edelman’s group in 1965, received a strong stimulus
from Putnam’s determination of the L-type light chain
structure. Another major input came from Porter's
group in London, when they reported on the heavy
chain structure of IgG from a myeloma patient and
from normal rabbit serum (Porter 1967). Porter and his
colleagues focused their efforts on that half of the heavy
chain where they believed the antibody’s antigen com-
bining site was located. The partial analysis he had com-
pleted by 1967 encouraged Porter to “claim that, if the
work. . .on the sequence of the heavy chains. . .can be
carried to completion, it appears to offer a feasible
experimental approach to obtaining an answer to the
question: does the amino acid sequence alone control
antibody specificity, and, if so, how is it achieved? ”
(Porter 1967, p. 425).

The achievements of groups such as Putnam's and
Porter's represented important pieces of the puzzle of
antibody structure, but its total solution required more.
If, as researchers now suspected, each immunoglobulin
molecule consisted of two identical light chains and two
identical heavy chains, a complete map of its primary
structure would be obtained by a sequence analysis of
one light and one heavy chain, and by locating all the
disulfide bonds and the various carbohydrate prosthetic
groups attached to the chains. »

This was the task that Edelman and five colleagues
at Rockefeller Institute had undertaken in 1965, a task
that would occupy ‘‘a good portion of [their] waking
hours” for four years (Edelman 1973, p. 883). Then, at
a scientific meeting in 1969 Edelman announced the
completion of their work. “We now report the amino
acid sequence fo an entire human [IgG] immunoglob-
ulin (molecular weight 150,000), the location of all
disulfide bonds, the arrangement of light and heavy
chains, and the length of the heavy chain [variable]
region” (Edelman, Cunningham et al. 1969, p. 78).

Within the scope of this essay we have come full
circle, for now, in 1969, immunologists had gained an
understanding of the primary structure of an antibody
molecule, and of how the variable and constant regions
in its heavy and light chains make possible an antibody’s
extraordinary specificity and its class or effector func-
tions. With this understanding the science of immunol-
ogy, that had begun in the 19th century with the work
of medical bacteriologists such as Louis Pasteur and
Robert Koch, underwent a major revolution. And, as we
have seen, a ‘‘crucial experiment of nature,” the long
puzzling proteins of multiple myeloma patients, occu-
pied center stage in the revolution. The quest to identify
the nature and origin of these proteins, begun by Dr.
Watson's query in 1845, had ended more than a century
later in ‘the first of the projects of molecular immu-
nology, the task of which is to interpret the properties
of the immune system in terms of molecular structures’’
(Edelman 1973, p. 830).

107

Those involved in the many facets of immunobiology
recognize that the molecular analysis of antibody
structure is only a beginning, albeit a profoundly impor-
tant one, in understanding the nature of the immune
system. The structural basis of antibody diversity" has
been revealed, but, as Gerald Edelman observed in his
1972 Nobel Prize address, ‘“two great problems of
molecular and cellular immunology remain to be solved.”
The first of these problems is “the origin of intrasub-
group diversity: what are the genetic mechanisms that
lie behind the enormous variability of amino acid
sequences within portions of the heavy and light chains?
(see note 11). The second problem, recognized since
Burnet proposed his clonal selection theory, is to explain
the induction of antibody synthesis: how is the clonal
expansion of lymphocytes triggered after their receptor
antibodies combine with antigens? Eventually, immu-
nologists are confident, these major questions too will
be answered, and immunology again will be transformed
“both as a discipline and as an increasingly important
branch of medicine’’ (Edelman 1973, p. 839).

 
 

1. Immunodeficiency diseases refer to those conditions,
frequently inherited, that are caused by various types of defects
in immunological function. Because a majority of patients with
inherited forms of immunodeficiency have been found to have
quantitative deficiencies of T cells, B cells, and their products,
the study of these diseases has had a major import for the devel-
opment of modern immunological concepts (see Bach and
Good 1972).

2. Like the B cell, the T cell has receptors on its surface
that can specifically recognize antigens. But, whereas the B cell's
response to an antigen is to produce antibody, the T cell releases
substances called lymphokines. The lymphokines, in turn, attract
monocytes (a type of white cell) which engulf and digest invad-
ers such as bacteria. The T cells also directly attack foreign
proteins.

3. The principal defensive or effector functions of each of
the five antibody classes are, briefly, as follows. /gM, the first
antibody to be produced in response to the presence of an
antigen, is evolutionarily the most primitive of the five types,
which perhaps accounts for its relatively weak binding ability.
IgM is involved in certain autoimmune diseases, such as rheu-
matoid arthritis. The major antibody type in mammals is /gG.
Both IgG and IgM act against foreign organisms and toxins, but
IgG has a more specific antigen binding ability and remains in
the blood much longer than IgM. IgG also is the only antibody
type able to cross the placenta, to confer passive immunity
from mother to fetus. /gA is present in large quantities in the
intestine, where it acts as a barrier to prevent the escape of
pathogenic organisms from the gut into the blood stream. The
known functions of /gE are primarily negative ones, from man's
perspective, as this antibody is responsible for triggering allergic
and asthmatic responses. The functions of the fifth type of anti-
body, /gD, presently are unknown (Lewin 1974, pp. 28-31).

4. An antibody’s structurally specific antigen binding site
results from how the amino acids are arranged in the variable
regions of its heavy and light chains, and the vast number of
possible binding site shapes are generated by permutations in
the possible sequences of the 108 amino acids that make up the
variable regions of both the heavy and light chains. Investigators
also have found that some areas of the variable regions are more
variable in amino acid sequences than others; these are termed
hypervariable regions.

5. The views of organic chemists in the 1840s on the nature
of albumin and protein were developed, most influentially, by
the work of Berzelius, Mulder, and Liebig on the elementary
analysis of albuminoid substances. Berzelius proposed the word
“protein” in 1838 to designate the ‘organic oxide of fibrin and
albumin,” and he felt that this “‘protein’’ was the ‘‘primitive or
principal stubstance of animal nutrition that plants prepare for
the herbivores, and which the latter then furnish to the carni-
vores.” Fruton notes that Berzelius’ and Mulders’ conclusions
about the identity of fundamental protein units were adopted
by the influential Liebig in 1841 “on the basis of analyses
performed by his associates Johann Joseph Scherer and Henry
Bence Jones’ (Fruton 1972, pp. 96-97).

Notes

108

6. For those interested in the nature and development of
clinical research, we note that multiple myeloma patients parti-
cipated in two different types of experimental work. First, some
patients had blood and urine samples collected for laboratory
analysis, or in vitro research. Secondly, some patients were
given substances, such as radioactively labelled glycine, and than
had blood and urine samples collected for in vitro study.

7. Good was at the Rockefeller Institute on a one-year
fellowship, having become interested in immunology through
his work as a pediatrician at the University of Minnesota. When
Good returned to Minnesota in 1950, he brought with him a
number of intriguing and puzzling clinical observations from his
year in New York. Among these was his learning from myeloma
patients that they had serious problems with infection. Why was
this the case, Good wondered, since these patients had such high
levels of plasma cells or antibodies in their blood, whose func-
tion is to combat infection. It was the pursuit of such clinical
puzzles that, among other accomplishments, would lead Good
and his colleagues at Minnesota in the 1950s and 1960s to
decipher the dual humoral and cellular system of immunity (see
Good 1972; Lewin 1974, ch. 1).

8. Other research groups besides those discussed in the
chapter also were conducting important research with Bence
Jones proteins, myeloma proteins and normal globulins in the
1950s, that would feed into the molecular analysis of antibody
structure. Among these groups were H. F. Deutsch and his
colleagues in the Department of Physiological Chemistry at the
University of Wisconsin, who worked on physicochemical and
immunochemical properties of myeloma and Bence Jones pro-
teins and of the macroglobulins found in patients with Walden-
strom’s macroglobulinemia (see Deutsch 1955; Deutsch et al.
1955, 1956; Morton and Deutsch 1958).

9. As part of their indirect template theory, Burnet and
Fenner in 1949 predicted the existence of immunological toler-
ance, a phenomena seen but not understood in 1946 when Owen
observed that most twin cattle are born with and retain a mix-
ture of each other's red blood cells. As part of their theory that
the body's recognition of self develops slowly during fetal life,
rather than being inherited, Burnet and Fenner predicted that an
antigen experimentally administered to an embryo would not
generate antibodies, but would be accepted as a normal part of
the embryo’s body. This state of ‘‘acquired tolerance’’ was
demonstrated in 1953, in experiments on tissue grafting by
Medawar and his colleagues. Medawar’s immunological research,
in turn, had developed out of his work for England's Medical
Research Council in the early 1940s on the problem of skin
grafts for W. E. Il burn victims. In 1960, Burnet and Medawar
received the Nobel Prize for their work on acquired immunity
(Burnet and Fenner 1949; Medawar 1944, 1945, 1957).

10. Edelman and Gally recognized that their use of myeloma
globulins to analyze immunoglobulin structure confronted them
“with a peculiar dilemma in structure-activity determination.
Either we commit a fundamental heresy in analyzing a myeloma
globulin the activity of which is unknown, or a structural heresy
in studying the amino acid sequences of an indeterminately
 

large mixture of specific antibodies.” Despite this dilemma, they
felt that the evidence for myeloma globulins being typical
immunoglobins permitted them to proceed with a ‘‘confident
analysis of the over-all structure of immunoglobins’’ (Edelman
and Gally 1968, pp. 329-330).

11. The discovery that the variable region of the antibody
molecule is responsible for the enormous range of structurally
specific antigen binding sites, as Porter observed in his Nobel
address, ‘‘raised very difficult problems as to the genetic origin
of these many different amino acid sequences’’ (Porter 1973,
p. 716). A now widely accepted explanation for the sequence
variability seemed at first a heresy, for it contradicted the one
gene-one polypeptide dogma established, as we saw in chapter 5,
largely through the analysis of abnormal hemoglobins. What
geneticists and immunologists accept as the most likely explana-
tion for the structure of antibody chains is a ‘two genes-one
polypeptide chain’ control mechanism, in which one gene
codes for the constant region and one for the variable region.
Two major explanations for a two-gene mechanism have been
advanced, the germ-line and the somatic mutation theories.
According to the latter theory, the multiple genes that code
for the variable regions are the product of somatic mutation of
a relatively small number of germ-line genes. (see Porter 1973;
Putnam 1969, 1972).

12. Following his work on the structure of light chains,
Putnam and his colleagues went on to ‘tackle the largest immu-
noglobulin of all, the IgM macroblobulin produced in large
amounts by patients with Waldenstrom’s macroglobulinemia’’
(Putnam 1972, p. 370). The task was a formidable one, for the
IgM is many times larger than IgG, with a molecular weight of
about 1,000,000, and has several other properties that also
complicated the task of analyzing its primary structure (see
Porter 1972, pp. 371-378).

109
 
 

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N

   

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114
CHAPTER 7 |
DISEASE AND DISCOVERY

The five case studies presented in this volume, as we
pointed out in chapter one, revolve around a common
theme that has been largely neglected in analyses of past
and present biomedical research: many paths of inquiry
and discovery about life processes have begun through
efforts to understand the nature of and to intervene in
states of disease. Although they focus, in current par-
lance, on the flow from categorical or disease-oriented
research to basic research and consequent advancement
of fundamental knowledge, rather than the more fre-
quently charted flow from basic research to clinical
application, these case studies belong to a larger body
of historical and sociological studies, and less directly,
policy studies, that have sought to articulate the pro-
cesses involved in various areas of research.

In the realm of policy-related studies, a number of
reports over the past decade have analyzed selected
examples of research-to-application developments in
biomedicine and other fields. Either explicitly or implic-
itly, these reports have been concerned with bolstering
a given position on the ‘proper’ allocation of federal
funds for “applied” or “‘basic’’ research, in response to
the debates engendered by President Johnson's call in
1966 to ‘‘zero in on the targets by trying to get our
knowledge fully applied’’ (see chapter one).

The first of these studies, commissioned by the
Department of Defense, was Project Hindsight, in which
a group of engineers and scientists retrospectively
analyzed the development of 20 major military weapons
(Sherwin and Isenson 1966).

Although it was issued only as a ‘‘first interim re-
port,” and despite methodological criticism of the short
historical time-span of the analyses and the validity of
transferring findings from the development of military
weapons to biomedical research, Project Hindsight’s
arguments for '‘targeted’’ research buttressed the new
policy climate in Washington vis a vis how federal sup-
port for research ought to be apportioned.

Given the strongly and widely held counter-ethos
among those engaged in biomedical research, affirming
the importance of ‘basic, undirected’’ research for
medical progress, it is scarcely surprising that Project
Hindsight triggered a series of rebuttals, in the form of

115

case studies documenting the role of basic research in
various medical innovations and other areas of techno-
logical advances. These included Shannon's account of
the development of the polio vaccine and Visscher's
study of the rubella vaccine, and the studies of various
technological innovations commissioned by the National
Science Foundation (Shannon 1967; Visscher 1967;
Illinois Institute of Technology 1968/69; Batelle/Colum-
bus Laboratories 1973). More recently, critiquing studies
such as the above for being either ‘anecdotal’ single
case reports or for being biased because the examples
were selected by those who did the analyses, Comroe
and Dripps used panels of consultants to help them
select and analyze the development of ten major ad-
vances in cardiovascular and pulmonary medicine and
surgery since the early 1940s (Comroe and Dripps 1974,
1976; see also Comroe 1977).

All of these post-Hindsight studies, particularly the
work by Comroe and Dripps by virtue of its methodo-
logy, argue persuasively for the importance of basic
research in the pursuit of greater knowledge about
disease states and diagnostic, preventive, and treatment
capabilities.

As historians of science and medicine, familiar with
a range of developments in many fields over many
centuries, we could not but argue that basic research
plays an essential role in shaping medical progress. Nor,
as we stated in chapter one, has this study sought to
argue otherwise. But, accepting the fact that research
proceeds in complex ways and by many routes, it would
be equally absurd to argue, as did an eminent biomedical
researcher in 1977, that “it has yet to be shown that
basic science progress can be a byproduct of applied
research’’ (Visscher 1977).

Such completely unidirectional statements, while
rare, reflect in part both stereotypic views about the
relationship between basic and applied research, and
the dearth of well-documented studies of how ‘‘im-
portant elements of the fundamental biomedical sci-
ences of the past have emerged from the study of
human beings and their diseases’ (Report of the Pres-
ident’s Biomedical Research Panel, App. A 1976,
p. 16).
The present study has been directed primarily toward
beginning to fill in this gap in the literature on biomed-
ical research. As such, whatever policy implications may
be read into it should be of a different order from the
Project Hindsight genre. For, we make no arguments
about, and draw no conclusions concerning, the relative
importance of basic or categorical research and in turn
the relative balance between the two broad categories
that should obtain in federal research funding. Indeed,
for reasons that we also explored in chapter one, we
have by and large avoided labelling the lines of research
that we examine in the case studies with terms such as
applied, categorical, mission-oriented, fundamental,
basic, etc.

From our perspective, if this study has any latent
policy ‘message’ it is to underscore the fact that scien-
tific knowledge and discoveries come from many sources,
by often unforeseen routes, and that we still know far
too little about the course and determinants of those
research processes that may variously result in thera-
peutic innovation or in fundamental knowledge. Here,
we concur with the views of a Rand Corporation report
for the President's Biomedical Research Panel concern-
ing the need for “improved conceptual frameworks of
scientific progress.” The report, characteristically,
focuses on the flow from basic to applied biomedicine
and notes only parenthetically that ‘questions arising
in an area of clinical medical science may become
important research questions for several areas of basic
medical science.” But, more generally, the repart ob-
serves that ‘‘as a practical matter, no analytical models
adequately capture the processes by which biomedical
R & D results flow into medical practice [or, we would
add, the converse processes]. The search for a single
comprehensive model that simultaneously has great
generality and great capacity to reflect the detail of
these processes is futile. Rather, the search should be
for a number of models of intermediate levels of gener-
ality, able to handle a wide variety of cases with adequ-
ate respect for their detail and complexity’’ (Report of
the President’s Biomedical Research Panel, App. B 1976,
pp. 77, 78).

Within the scope of this study, however, we have not
attempted to construct an analytical model for the flow
from categorical to basic research, nor to test existing
models of the flow from basic research to medical
practice to see how well they can incorporate the
“reverse lines’ that we have traced in our case studies.
Neither, and this would be perhaps the more intellectu-

116

ally satisfying and ultimately useful task, have we
examined fully the types of research and discovery
processes that we have analyzed in relation to various
philosophical and sociological theories about the nature
of science, as one of us has attempted to for neuro-
science research (Swazey and Worden 1975).

All three types of model building and testing are
needed to help us better understand how categorical
research can contribute to basic science research, and to
better understand the nature of scientific research and
discovery more generally. Such efforts, however, will be
sounder when there is a larger body of detailed case
studies, whether of the sort in this volume or the types
sponsored by the NSF or conducted by Comroe and
Dripps.

The type of historical analyses we have done, as we
have noted, is only one of several possible approaches,
one we used because of our particular shared training in
the history of science, and because one of us has found
the detailed case study format a particularly congenial
and fruitful mode of historical and sociological analysis
(Swazey 1969, 1974; Fox and Swazey 1974; Worden,
Swazey, and Adelman 1975).

A particular merit that we find in the case study for-
mat is that it can reveal and illustrate many processes
and phenomena involved in research. Thus, each of our
cases does more than document the fact that categorical
research can contribute in significant ways to the ad-
vancement of basic knowledge.

The other phenomena and patterns that the cases
illustrate include, first, the nature of serendipity, a
phenomenon we discussed at some length in chapter
one in relation to its frequent misinterpretation as a
discovery resulting from a totally fortuitous event, and
its invocation as the distinguishing characteristic of basic
research. As we noted, more careful historical and
sociological analyses show that serendipity involves far
more than chance - that, in Pasteur’s famous dictum,
chance favors the prepared mind - and that there is no
inherent reason why serendipity should occur only in’
basic rather than applied or categorical research. Both of
these points are borne out, once again, in the instances
of serendipity recorded in our case studies: for example,
Pasteur’s observation of fermentation in the solution
of racemic ammonium tartrate lying in his laboratory;
Eijkman’s pursuit of the sudden outbreak and equally
sudden disappearance of polyneuritis in his chickens;
Minkowski’s discovery that the removal of a dog's pan-
creas caused diabetes mellitus; and Ingram’s decision

 

 
to study the protein chemistry of sickled cells.

A second point about research that we addressed in
chapter one was the problems that commonly ensue
when, for heuristic, policy, or other purposes, one tries
to neatly /abel a given research activity as basic, applied,
mission-oriented, fundamental, etc. These problems are
seen in this volume as one thinks about the work on
thiamine's structure and functions by researchers such as
Williams and Peters, the study of minimal diets by
Hopkins, McCollum, and others, the many reasons that
the strange proteins of multiple myeloma were studied
in the 1950s, and, perhaps preeminently, in the work of
Louis Pasteur on the diseases of wine and vinegar.

Another frequently discussed factor in scientific and
technological advances is the role of technique, embrac-
ing both methods and instrumentation. Technique, not
surprisingly, played an important role at many junctures
in our cases. To recall but a few examples: technique
helped to resolve competing theories, as was the case in
surgical and aseptic techniques in endocrinology and
with Pasteur’s experimental denunciation of the sponta-
neous generation theory; permitted the identification of
a new substance, the beriberi ‘‘vitamine,”” by means of
improved assay, extraction, and purification; and de-
tected the molecular basis for sickle cell anemia by
“fingerprinting’’ the hemoglobin molecule.

The case studies also illustrate the important role that
interdisciplinary fusions played in many of-the advances
we charted. As exemplified by the development of
endocrinology as a field of research and the subsequent
emergence of neuroendocrinology, and by the enormous
yield of the mergers of genetics, microbiology, and
biochemistry that engendered molecular biology, the
coming together of different disciplines, with a new
sharing of perspectives, interests, and methods, is an
important pattern in the course of research and discov-
ery.

Another common and important pattern in research
seen in our cases, a pattern that has been analyzed in
detail by Comroe, is the occurrence of /ags, which may
be of various types and occur for various reasons (Com-
roe 1976). In the delays that ensued in the acceptance
of the concepts of gene action put forward by Mendel,
Garrod, and Beadle and Tatum, for example, we see
instances of lags that occurred in part because of the
persistent feeling, in Beadle’s words, ‘‘that any simple
concept in biology must be wrong.” The conflict of a
new finding or theory with prevailing views also can
cause lags in acceptance and utilization, as was partly

 

the case in biochemical genetics and as occurred in the
resistance that the Scharrer’s concept of neurosecretion
encountered. Here, we see elements of the pattern of
resistance by scientists to scientific discovery, a pattern
that has been examined in detail by sociologists, histo-
rians, and philosophers of science (see Barber 1961;
Frank 1961; Kuhn 1970). Depending on their nature
and consequence, as Comroe points out, lag times in
research between discovery and rediscovery, discovery
and acceptance, discovery and application, etc., may
be too long, too brief, or of an appropriate duration.
Thus, for example, what may seem at first to be an
unduly long period of time between a discovery and the
understanding of what that discovery means, as in the
over 100 years between the discovery of Bence Jones
proteins and their identification, may turn out to be
an appropriate “latency’’ period when one examines the
knowledge and technique prerequisite to the proteins’
characterization.

The case studies further bear upon several questions
about the development of theories that have long drawn
the attention of those interested in the nature of science,
and engaged them in often intense debates. In traditional
formulations, briefly, science is viewed as an ‘objective’
endeavor that uses the cutting “edge of objectivity’’ to
separate truth from error. Traditional accounts of the
nature of science, such as those perpetuated in text-
books, also place strong emphasis upon the value of
hypothetico-deductive thought, the use of experimenta-
tion, and the scientist as one who ‘‘does not blindly
accept established dogma’ (Brush 1974; Gillispie 1960).

Another major component of traditional views of
the nature of science is that science progresses incre-
mentally, adding each discovery, like a new brick, to
previously laid bricks in the slowly rising edifice of
“truth.” This image of science, as Ragnar Granit has
noted, is reflected in one of the most prestigious sym-
bols of scientific achievement, the Nobel Prize. “The
young scientist often seems to share with the layman the
view that scientific progress can be looked upon as one
long string of pearls made up of bright discoveries. This
standpoint is reflected in the will of Alfred Nobel, whose
mind was that of an inventor, always loaded with good
ideas for application. His great Awards in science presup-
pose definable discoveries’ (Granit 1972, p. 3).

Without asserting that science never operates in the
ways outlined above, views contradicting traditionally
accepted accounts have long been offered by scientists
themselves, as well as by philosophers, historians, and

 
sociologists; perhaps the most influential and controver-
sial “unorthodox” account in recent years has been
Thomas Kuhn's analysis of the structure of scientific
revolutions (Kuhn 1970; Lakatos and Musgrave 1970;
Scheffler 1967; Swazey and Worden 1975).

One recurring pattern seen in our case studies that is
particularly relevant to these varying interpretations of
the nature of science, and on balance favors views such
as Kuhn's, concerns the ways that scientific theories
develop. Scientific theories, according to the canons of
experimental science, arise out of data, and stand or fall
solely on the basis of objective scientific evidence. To
this thesis our case studies, as have many others, say
“not so.” We have, for example, already noted the types
of resistance by scientists to new discoveries or theories,
a recurring pattern that argues against the ‘“‘edge of
objectivity.” Prevailing theories, secondly, may deter-
mine, at least for a time, the type of evidence that
researchers seek, or the explanation they offer for a
particular phenomenon. Thus, in two of our cases, we
saw how the infectious disease model was applied to
both the explanation of beriberi and the search for its
cure, and to the view that the ductless glands function
to neutralize or remove toxins in the blood.

Correlatively, we have encountered a number of the
classic theoretical controversies that run throughout
the history of science and medicine. These include
Pasteur’s engagement in the long debate over spontane-
ous generation; the competing theories of endocrine
function in the late nineteenth and early twentieth
century; debates over the nature of what came to be
known as vitamins; the long and often heated battle
between proponents of humoral and cellular theories
of immunity; and the play between selective and instruc-
tive theories of antibody formation. The resolution of
such controversies involves more than just the accumula-
tion of new scientific evidence or what Kuhn calls ‘‘the
methodological stereotype of falsification by direct
comparison with nature’ (Kuhn 1970, p. 77). Rather,
as Kuhn argues, historical studies of scientific develop-
ment indicate that ‘the act of judgment that leads a
scientist to reject a previously accepted theory is always
based upon more than a comparison of that theory
with the world. The decision to reject one paradigm is
always simultaneously the decision to accept another,
and the judgment leading to that decision involves the
comparison of both paradigms with nature and with
each other” (Kuhn 1970, p. 77).

118

Finally, in this brief consideration of the relationships
between scientific theories and data, scientists them-
selves have often made an ‘‘unorthodox’ admission:
their decisions as to what and how they will observe, as
well as how they may subsequently interpret those
observations, are predicated by their theoretical con-
structs, rather than vice versa. One of the best expres-
sions of this way of ‘‘doing science’’ was made by Albert
Einstein in 1926, when he responded to Heisenberg’s
statement that only observable magnitudes must be used
in formulating a theory like that of relativity.

Possibly | did use this kind of reasoning, but it
is nonsense all the same. Perhaps | could put it
more diplomatically by saying that it may be
heuristically useful to keep in mind what one has
observed. But on principle, it is quite wrong to
try founding a theory on observable magnitudes
alone. In reality the very opposite happens. It
is the theory which decides what we can observe.
(quoted in Brush 1974, p. 1167)

Three comparable counter-instances to traditional views
of doing science come at once to mind from our cases.
Pasteur’s preconceived and strongly held ideas about the
role of molecular dissymmetry in the ‘“‘organization of
living organisms’’ both helped lead him to search under
his microscope for living organisms in ferments, and
structured many of his interpretations of his observa-
tions. Linus Pauling and his colleagues came to their
analysis of sickled cells with Pauling’s concept of “mole-
cular disease’’ already in his mind, a concept triggered
when he first discussed sickle cell anemia with William
Castle in 1945 and related what he learned to his prior
work on the nature of antibodies. Thirdly, reflecting in
his Nobel Prize address on his and Tatum’s experiments
with Neurospora, George Beadle said, much as had
Einstein: “It is sometimes thought that the Neurospora
work was responsible for the ‘one gene-one enzyme’
hypothesis. . .The fact is that it was the other way
around - the hypothesis was clearly responsible for the
new approach.”

For us, in sum, Today’s Medicine, Tomorrow's
Science does more than chart the ways that the study of
disease problems can lead to new vistas in our knowledge
of basic biological phenomena. We do not claim to have
made ‘‘discoveries’’ in this study, as that term is com-
monly understood to mean new and unexpected find-
ings. But if, as Ragnar Granit suggests, the real goal of a
 

researcher's labors is understanding or insight, rather
than the ‘eureka’ of discovery, it is hoped that these
essays have contributed to our understanding of the
complex enterprise that is biomedical research.

 
 

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