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From Schizomycetes to Bacterial Sexuality
A case study of discontinuity in science

Joshua Lederberg and Harriet A. Zuckerman

I.   Introduction

    This case study in scientific biography is intended to examine
the process of scientific growth and discovery by joining the assets
and skills of a participant-reminiscer with those of a more detached
behavioral scientist.  The particular arena of interest is the
convergence of genetics with bacteriology that attended the work of
Lederberg and Tatum in 1946. At the time we began in 1973 there were few
precedents for such a self-conscious collaboration. A similar
collaboration which examines the development of radio astronomy in
Britain after World War II has recently culminated in "Astronomy
Transformed" by David 0. Edge and Michael J. Mulkay (New York: Wiley,
1976).

   For the past 30 years bacteria have been favored objects for
research on DNA.  Together with their parasitic viruses, the
bacteriophages,  these simple organisms continue to offer indispensable
advantages for seeking deeper insight into the chemical basis of
heredity,  and for bringing such knowledge to practical application. The
importance of bacteria as agents of infectious disease, clearly
established by 1876, might also be thought to have accelerated
inquiries into their basic biology. Paradoxically, the opposite may
have been true,  as will be discussed further in section III.

But before bacteria could be routinely accepted as paradigms of
research in terrestrial biology, the question of whether "bacteria have
genes,  like all other organisms" had to be clarified. The crucial
experiment was conducted at Yale University in 1946 by Joshua Lederberg
(1925-     1,  and E.L. Tatum (1909-1975).{ 1 }

   Their approach was to demonstrate genetic recombination - the
exchange of genes between different cells - in a typical bacterial
species like Escherichia coli. Existing dogma in microbiology held that
bacteria could not be crossed. They reasoned that if a sexual mode of
reproduction  occurred in bacteria at all,  it might be quite a rare
event.  Therefore, particular attention was paid to an efficient
selective design,  the genetic characteristics of the input strains
being arranged so as to make it easy to detect even the very rare
occurrence of new recombinant types. In these experiments,
biochemically defective mutants,  whose ability to grow could be
manipulated by altering the composition of the growth medium, proved to
be especially suitable research material. Tatum's recent work with
Beadle had established the feasibility of preparing such mutants and
their advantages for a wide variety of investigations, in a fungus,

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Neurospora,  whose genetics was already well established. The
production of similar mutants in bacteria, which Tatum had pioneered,
was now to be the Ariadne's thread to lead them back to an
understanding of the genetic structure of these organisms.

   Their basic design was to establish two different, complementary
mutant strains requiring different nutritional factors. Neither of them
would be able to grow alone, in a selective synthetic  medium. Thus
genetic recombinants, no matter how rare,  can be detected by plating
large numbers of bacteria grown together into this medium. Typically,
one may plant a billion organisms in a single Petri dish, and recover a
hundred recombinant colonies. These methods, and the target strain E.
coli K-12 have become standard for contemporary research in bacterial
genetics, as recited in several hundred new publications a year.
   Our elaboration of this 1946 discovery traverses Lederberg's

autobiography of his entree into research; the history-of-ideas of the
problem (which was more difficult to perceive than to solve); and some
sociological observations on a series of issues raised by these
accounts. Recognizing the difficulty of systematically communicating a
tangled web of facts,  commentary and criticism, we hope this pattern of
ever-widening perspective may be helpful to readers of diverse
persuasions.

   The following sections are in fact the fruit of a collaboration in
which the conventionalized roles of the participant in the historical
event and of the interviewer-scholar were repeatedly redefined as each
of us tried his hand at the tasks of the other. In nearly all oral
histories of science,{ 2  } the scientist participant responds to
questions by the interviewer who has reviewed the relevant documents.
Our procedure differs in several important respects: first, our effort
was iterative

-- new possibilities suggested in the course of discussion led to
renewed search for apposite material; and second, these searches (made
by the participant as well as by the interviewer) consulted archival
materials both personal and public,  and other individuals knowledgeable
about our problem. In the process, both authors learned a good deal
about the other's perspectives.

   This iterative procedure evolved gradually; but one constant
element in our inquiry was the conviction that personal reminiscence,
though indispensable, had to be corroborated by contemporary documents
or other testimony.{ 3 } As professional historians know, documents
(especially multiple documents) can confuse as well as illuminate
events.  Moreover,  it now is clear that accounts of the same discovery
by different participants do not square very well with one another
owing to their unique perspectives on the event.{ 4  ) Autobiography
is especially prone to what Kurt Stern calls "retrospective memoryI (52
and particularly deserves the constraints imposed by documentation.

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    II. Personal history - an inside story
This section is presented in the first person by Joshua Lederberg,

to help convey impressions and inf
personal recollection. However the air ation which are asseverated by
                          arrative is so profoundly informed
by critical dialogue with my co-author that it is scarcely pure
autobiography.

   The pivot of my account is September 1941, when I enrolled as an
entering undergraduate at Columbia College in New York City. My earlier
education  was framed by the New York City public school system:
especially by the cadre of devoted and sympathetic teachers who went
far beyond their duty in encouraging a precocious youngster whose
demands they could not always meet from their own knowledge, and the
llelitistlV high school system as represented by Stuyvesant High School -
open by competitive examination to students with a bent for science and
technology.   Even more important perhaps was the local Washington
Heights branch of the Carnegie-New York public library system. These
institutions symbolized and embodied the melting pot ideology. My
father was an orthodox rabbi, born and educated in Israel, and thus had
more prestige,  possibly higher aspirations for his children, and less
income  than most of our neighbors.  Like many other first-generation
Jewish youths in New York City at that time, I was recruited into an
efficient and calculated system of Americanization, fostered by the
rich opportunities and incentives of the educational system.

   My earliest recollections  aver an unswerving interest in science,
as the means by which man could strive for an understanding of his
origin, setting and purpose,  and for power to forestall his natural
fate of hunger, disease and death.  This may have been the most
acceptable deviation from the religious{ 6  } calling of my family
tradition. It was  reinforced by the role of Albert Einstein and Chaim
Weizmann as culture heroes - heroes whose secular achievements my
parents and I could understand and appreciate regardless of the
intergenerational conflicts evoked by my callow agnosticism and
ostentatious rejection of the orthodox Jewish ritual. The Jewish faith
is remarkably tolerant of skepticism,  and the set of mind thus
encouraged may have carried over into my reflex responses to other
sources of authoritative knowledge.

   The library was my university as I went through grade school and
junior high school. My most prized Bar-Mitzvah present was a copy of
Bodansky's "Introduction of Physiological Chemistry".{ 7 ) I had
already devoured Bodansky at the local library along with hundreds of
other works in the sciences, mathematics, history, philosophy and
fiction.  Books by Jeans, Eddington and especially Wells, Huxley and
Wells'  encyclopedic  'The Science of Life'  were the most influential
sources of my perspective on biology and man's place in the cosmos,
seen as evolutionary drama.

   Stuyvesant High School offered unusual opportunities for practical
work in machine shops and analytical laboratories as well as straight
classroom teaching.

   Having begged for and been granted access to the Cooper Union
Library (near Stuyvesant),  I had also read many research papers - but
neither these, nor my teachers could really  say much of the life of
the scientist at work.

   Playing at research in high school and then for some months at
the American Institute's Science Laboratory (a predecessor of the
Westinghouse Science Search) did focus my  interests in chemical
cytology; and I entered Columbia with the idea of learning the

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chemistry of cellular components so as "to bring the power of chemical
analysis to the secrets of life". I looked forward to a career in
medical research where such advances could be applied to problems like
cancer and the malfunctions of the brain.

  My curriculum at Columbia was somewhat unconventional. As soon as a
dubious bureaucracy would permit,  I registered in a number of graduate
courses in the Department of Zoology. Not until my last term had I
matured enough to seek and profit from a rounding of my humanistic
education at the hands of teachers like Lionel Trilling and James
Gutman.

   Professor H.B. Steinbach, who taught the introductory Zoology 1
course, helped arrange a laboratory desk in the histology lab where I
could pursue some small research of my own.  I became interested in the
cyto-chemistry of the nucleolus in plant cells, hoping to develop new
staining methods that could reveal its composition.   The then recent
publication of McClintock and Rhoades on the genie control of nucleolar
synthesis in maize also introduced me to the power of genetic analysis
in cell biology.

   Professor Franz Schrader's course in cytology introduced me to
some of the problems of mitosis.  I became curious about how the drug
colchicine interferes with the mitotic spindle.  Herein was my first
(trivial)  "discovery":  an apparent gradient of susceptibility to
colchicine down the onion root meristem; but there was no way to
determine whether this was an intrinsic difference in the cells, or a
transport problem.

   This work led to two other starts:  (1) an effort to induce
chromosome aneuploidy in mice by the application of limiting levels of
colchicine during spermatogenesis, and (2) a broader inquiry into the
effects of narcotics and other specific inhibitors on the mitotic
process.  It was easy to disrupt spermatogenesis with colchicine; I saw
giant (presumably polyploid) spermatids, but I was unable to verify the
successful maturation of these peculiar cells. The matter has never
been satisfactorily investigated and may still be of some importance as
a prototype of teratogenesis from environmental causes.

   The problem of the cytophysiology of mitosis led me to specialize
in courses in cell physiology.However, at that time this was
preoccupied primarily with energy metabolism. I learned little that
appeared to be useful for the problems of protein synthesis and fiber
assembly in mitosis.

   I first met Francis Ryan in September 1942, when he returned from
his postdoctoral fellowship at Stanford University with E.L. Tatum to
become an instructor in Zoology.  He brought back the new science of
Neurospora biochemical genetics  and a gift of inspired teaching that
was to be a decisive turning point  in my own career.   I had little or
no contact with him in formal courses, but by January 1943 I was
working in his laboratory assisting  in the preparation of media and
handling of Neurospora cultures.  For the first time I was able to
observe significant research as it was unfolding and to engage in
recurrent discussions with Francis - and with an ever widening group of
graduate students in the department - about Neurospora, life, and
science.

   Hitler achieved power in Germany when I was eight years old - just
old enough to have no doubt about the eventual outcome  of his march
across Europe.  Eight years of fascinated horror at the unfolding of
history followed -- the persecution of the German Jews, the flight of
intellectuals like Albert Einstein,  the occupation of Austria, Munich,

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the Nazi-Soviet pact and partition of Poland, the fall of France, the
victory of the RAF over Britain,... Pearl Harbor. We knew that the War
would dominate our lives until a painful victory was won. The actual
disposition of our efforts was in the hands of a slowly evolving
bureaucracy. Awaiting the final call to military service, most of us
simply continued our daily pursuits speculating when we would be called
upon in our particular fashion.

  My own response was to enlist in the Navy V-12 college training
programs upon  reaching my 17th birthday, well before I was eligible
for the draft. This opened the door to further training for
commissioned rank. Fortunately, Columbia College contracted with the
Navy among the services,  and when V-12 was called to active status on
July 1,  1943, I could continue  my studies at the same institution! {E}
The V-12 curriculum was designed to
compress pre-medical training to about 18 months of
instruction, and the I-year M.D.  curriculum into 3 calendar years. We
also got a modicum of Naval officer-candidate preparation and physical
education, leaving little time for extra-curricular research.
  My further months at Columbia College were alternated with spells

of duty at the U.S. Naval Hospital, St. Albans, L.I. Here I was
assigned to the clinical parasitology laboratory. The practical use of
my previous training in cytology was the examination of stool specimens
for parasite ova,  and the routine examination of blood smears for
malaria among the Guadalcanal veterans of the First Marine Division.
This gave an opportunity to look for the chromosomes of Plasmodium
vivax.  The "chromosomes" were so tiny and the Feulgen staining so faint
that it is difficult to insist on the reality of those observations.
However, this experience informed me of the sexual stages of the
malaria parasite, and this undoubtedly sensitized me to the possibility
of cryptic sexual stages in other microbes (perhaps even bacteria.)

   In October 1944 I was reassigned to begin my medical course at
Columbia College of Physicians and Surgeons. As a medical student, I
attempted to continue research studies on the control of mitosis:
namely a search for a hypothetical humoral factor that regulated the
size of the regenerating liver after partial surgical excision. With a
fellow student, Anthony Iannone, I performed some encouraging
parabiosis experiments. However, neither the available assay methods
nor our surgical skills and facilities approached what was needed for
the task. First year medical students at P&S were not, in any case,
encouraged to do research and my intellectual and social environment
continued to center on the Morningside Heights campus.

   The important biological discovery of 1944 was the identification
by Avery, McCarty and MacLeod of the substance responsible for the
pneumococcus transformation.{ 9  } This phenomenon appeared to be the

transmission of a gene from one bacterial cell to another; but this
interpretation was inevitably dimmed by the level of general
understanding of bacterial genetics at that time. Avery's findings were
promptly communicated to Columbia by Dobzhansky (who visited
Rockefeller) and by Alfred Mirsky (of the Rockefeller faculty) who was
a close collaborator of Arthur Pollister in the department .   The
Rockefeller work was the focus of widespread and critical discussion
among the faculty and students there. Mirsky was a vocal critic of the
chemical identification of the transforming agent. I believe he was
essentially persuaded that this was an instance of gene transfer, but
he was not yet prepared to concede that the evidence to date settled
so important a question as the chemical identity of the gene as pure

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DNA (versus a complex nucleoprotein).

My information about Avery's work was second-hand until I actually read
the paper on January 20,  1945 at Harriett Taylor's urging. At that time
she had already arranged to pursue her postdoctoral studies with Avery
at the Rockefeller Institute after she completed her Ph.D. that spring.
My immediate response is recorded as " .., unlimited in its
implications... Direct demonstration of the multiplication of
transforming factor... Viruses are gene-type compounds [sic]
. . .  excruciating pleasure of reading."

   What could be done to incorporate this dramatic finding into the
main stream of biological research;  how could one further advance these
new hints about the chemistry of the  gene ? One answer to this urgent
question that occurred to me would be to attempt a similar
transformation by DNA in Neurospora. Not only did this organism have a
well understood life-cycle and genetic structure. It also had the
advantage of being amenable to selection for rare nutritionally
self-sufficient (prototrophic forms) which would facilitate the assay
for the transformed cells.

   Sometime between January and May,  1945, I brought this suggestion
to Francis Ryan who replied that he had been speculating along somewhat
similar lines,  and that he would be glad to have me work with him on
the question. As a brief vacation was looming
(to follow rigorous examinations in Anatomy) we agreed that we might
begin in June,  and so we did. However,  we soon discovered that the
Neurospora mutant would spontaneously revert to prototrophy. We did not
therefore have a reliable assay for the effect of DNA in Neurospora.
However,  the details of the reverse mutation phenomenon resulted in my
first scientific publication {50].

   Questions about the biology of bacteria would then continue to
fester so long as bacteria remained inaccessible to a conventional
genetic analysis for lack of a sexual stage. But was it true that
bacteria were asexual? Some of the more sophisticated textbooks and
especially Dubos' monograph,  'The Bacterial Cell'{ 10 ) ,   indeed had
footnotes indicating the inconclusive status of claims for the
morphological exhibition of sexual union between bacterial cells.
Little genetic testing of this hypothesis had been done. Another
important input to this intellectual confrontation was an appreciation
of sexuality in yeast, via the graduate research work of Sol Spiegelman
and Harriett Taylor. Yeast is at least superficially a closer analogue
to bacteria.  It had long been known that yeasts produced spores
through a sexual process, but the occurrence of clear-cut mating types
in yeast had not been demonstrated until 1935 by Winge( 11  } and then
further exploited for genetic analysis by Lindegren and Spiegelman.
These successes only dramatized the importance of finding a sexual
stage if it existed,  in a variety of microbes.
   Some of my notes dated July 8, 1945 articulate - on neighboring

pages - hypothetical experiments involving (a) a search for mating
between the medically important yeast-like fungi, the monilia and then
(b) the design of experiments to seek genetic recombination in bacteria
(by the protocol that later proved to be successful). These notes also
coincide within a few days, with the beginning of my course in medical
bacteriology at medical school.  They may have been provoked by the
repeatedly asserted common wisdom that bacteria were "Schizomycetes",
asexual primitive plants.

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   Dubos's monograph cites a host of muddled, and two clear-cut,
studies (Gowen and Lincoln, Sherman and Wing) intended to look for
genetic exchange in bacteria by the methodology of genetic exchange.
But even  these two instances lacked the advantage of any selective
method for the detection of recombinants.  Therefore they would have
overlooked such a process if it occurred less often than perhaps one
per thousand cells.

  Within a few days I set out on my own experiments along these
lines -using  in the first instance a set of biochemical mutants in
bacteria which I began to accumulate in Ryan's laboratory.

   Meanwhile at Stanford Ed Tatum, whose doctoral training at
Wisconsin had been in the biochemistry of bacteria, was returning to
bacteria as experimental objects,having published two papers on the
production of biochemical mutants in E.  coli.{ 12 ) During that
summer of 1945 Francis learned that Ed was
about to move from Stanford University to
set up a new program in microbiology at Yale.  He suggested that rather
than ask Tatum merely to share his newly founded collection of
bacterial mutants, I should ask to work directly with him and get the
benefit of his detailed experience and general wisdom. The war was
nearing a victorious conclusion;  civilian life and academic schedules
might soon be  renormalized and make such a visit possible. With this
encouragement, I then wrote Tatum of my research plan (Fig. 1 ) and
applied for such an accommodation. Dean Aura E.  Sevringhaus of P&S also
approved such a visit as qualifying for an elective quarter offered to
medical students during their third year of study.

  Tatum congenially agreed and suggested that I arrive in New Haven
in late March, to give him time to set up his laboratory. I had some
hint that he may have been formulating similar experimental plans, but
these were never pressed upon me. This arrangement suited him by
leaving him free to complete his current work in the biochemistry of
Neurospora, and still follow up the long shot gamble in looking for
bacterial sex.

   It took about six weeks from the time the first serious efforts at
crossing were set up in mid-April 1946 to establish well-controlled,
positive results and by mid-June Tatum and I felt that the time was
ripe to announce them. A remarkable opportunity was forthcoming at the
international Cold Spring Harbor Symposium. This year, it was to be
dedicated to genetics of microorganisms, signalling the postwar
resumption of major research in a field that had been invigorated by
the new discoveries with Neurospora, phage, and the role of DNA in the
pneumococcus transformation. Tatum was already scheduled to talk about
his  work on Neurospora. Happily, we were also granted a last minute
insertion into the program (ca.  July 11) to permit a brief discussion
of our new results.

   The discussion was lively ! The most contentious criticism was
Andre Lwoff's concern that the results might be explained by
cross-feeding of nutrients between the two strains without their having
in fact exchanged genetic information. Having taken great pains to
control this possibility,  I felt that the indirect evidence we had
gathered should be accepted as conclusive, and there was more time
spent than necessary in argument whether more direct proofs should be
furnished that the purported recombinants were indeed pure strains.
Fortunately, Dr. Max Zelle took me aside after the meeting and most
generously offered to advise and assist me in the direct isolation of
single cells under the microscope. These subsequent observations did
quiet remaining concerns of the group at the Pasteur Institute that

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Lwoff had assembled ,e.g. Jacques Monod, Francois Jacob, Elie Wollman,
which was to make the most extraordinary contributions to the further
development of the field. These single cell methods were also most
useful in later investigations in several directions.

   The most gratifying evidence of the acceptance of these claims by
my scientific colleagues was the trickle (later a torrent ) of requests
for the cultures of E.  coli K-12 to enable others to  repeat the
experiments. The first significant publications of this kind  came from
Dr. Luca Cavalli-Sforza, originally from R.A.  Fisher's laboratory at
Cambridge and later from Milan and Pavia.  This prompted the beginning
of an extended transatlantic (and now collegial) collaboration which
was most gratifying from both the scientific and personal standpoint.

   The tribute that is owing to Francis Ryan and Ed Tatum needs a
larger frame than this article to be justly recorded. At a time when
the public image of scientific fraternity is so problematical,   it is
important to record the survival of norms{ 13  ) and behavior
exemplifying mutual respect, helpfulness, consideration, and above all
a regard for the advance of knowledge, even in a system that inevitably
puts a high premium on competition and self-assertion. I have never
encountered the extremities that Jim Watson painted in his
self-caricature of ruthless competition (The Double Helix), which is
hardly to argue that they do not take place. However, even by the most
optimistic normative standards, the generosity and selflessness of my
own teachers stand out as examples to be emulated, and to pass on to
those whom I might in turn have the privilege to influence. Perhaps the
greatest tribute to their skill as teachers is that they have made it
impossible, to this day, for me to dissect my own innovation and
creativity from the ideas that they may have planted and certainly
nourished in the course of my learning and collaboration with them.

   Since 1946, E. coli K-12 has been the subject of innumerable
investigations, some of which have substantially revised and enlarged
our first simple models of the sexual behavior of E. coli (19) . The
detailed story of the ripening of the initial discovery is an example
of international cooperation and competition that deserves a richer and
better informed treatment than is possible here.

   The main burden of the present article is not only to examine how
the discovery was attained in 1946, but also to ask more sharply: Why
then?" --or perhaps even more pointedly,  "Why not many years earlier?".
From a purely technical standpoint, equally decisive experiments might
have been conducted say in 1906, at a time when the rediscovery of
Mendelism had swept the imaginations of every other biological
discipline. Could we say that the 1946 discovery was postmature?
   These are not questions that can be answered with the precision of

research on mechanisms of cell biology, but we believe they demand
examination for reasons that go far beyond idle curiosity.  They are
vitally important to the self-criticism of science with respect to the
efficiency with which its avowed aims are pursued. For some groping
towards a better understanding,  we will now turn to a review of the
historical context of the understanding of bacterial life cycles prior
to 1946.

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III. Intellectual History of the idea of Bacterial Asexuality

   This 'history of scientific thought', prior to 1946, emphasizes
factors that may have discouraged inquiries into sexual processes in
bacteria.

   Bacteria were first noticed as objects of scientific microscopy by
van Leeuwenhoek on May 26,1676. However, the limitations of the
microscope and of cultivation technique hindered the delineation of
their life histories for two centuries. Bacteria assumed the image of
a crucial link in the
"Chain of Being", the bridge  between inanimate and animate forms of
matter. This image was highlighted in the "spontaneous generation
controversy":  what could be better substantiation of the reduction of
biology to mechanistic laws than the demonstration of the spontaneous
(re-)generation of living forms from inanimate matter?

  By 1861 the experiments of Louis Pasteur had displaced  the
commonsense observation of "spontaneous" putrefaction with the now
prevalent view that the atmosphere and other natural media are almost
universally contaminated, so that special precautions are needed to
demonstrate the continuity of microbial life from pre-existing spores
and cells. Together with the persistence of the Chain of Being image,
the phobia of contamination was to play an important role in the
further development of bacteriology.

   In 1875, Ferdinand Cohn published a definitive taxonomic system of
bacteria and coined the epithet Schizomycetes to categorize the entire
group.  This label,  WVfission-fungil', reinforced Cohn's categorization of
the place of bacteria in the living world. These were not
parabiological apparitions; they were simply primitive plants which
lVonly reproduce by asexual means", a view that was hardly challenged
for 70 years. This doctrine was no mere arbitrary whim; it was a
reaction both to the doctrine of spontaneous generation and to the
equally fantastic claims of interconvertibility of bacterial forms and
of complex life cycles. To Cohn's mind, such claims   resulted from
contamination and  faulty technique that would dangerously confound the
newly clarified taxonomy of bacteria based on stable pure lines.{ 14   )

  Medical microbiology could not have emerged as a science without
the doctrinal base laid down by Cohn and the pure culture  methods of
Robert Koch. The identification of specific bacterial species as the
causes of specific infectious diseases made it a matter of the highest
practical as well as theoretical urgency to reject preparations,
ideologies or results that might be subject to contamination.

   This new view rapidly solidified as the "Cohn-Koch Dogma" of
Monomorphism: "Each species of microbe is unchangeable in form and in
properties and cannot transform into another species". (Henrici 1934,
p. 19).  It dominated both the German and the French schools of
bacteriology and, by the 1890's,  the notions that bacteria could
reproduce sexually and that  variability(if it occurred at all) might
result from sexual mating were unthinkable for most bacteriologists.
The problem of bacterial variation thus acquired an unsavory reputation
or image. (See Lohnis 1921, pp.  l-30 for a review of evidence for
monomorphism and polymorphism).

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   This attitude toward studies of variation may be described as a
reaction formation that for many years averted bacteriologists from the
systematic study of bacterial variation.  In the practical sphere,
genetic variation served mainly to thwart utilitarian objectives-the
reliability of a vaccine, or the proof of the etiology of a newly
studied disease. Variation would tend to be dismissed as a nuisance

-- even today industrial microbiologists bewail the
"degeneration" of their stock cultures -- rather than be confronted as
a challenge to scientific insight. The preeminence of utilitarian
motives in bacteriological work (be it medical, foods, agricultural or
industrial) probably gave more weight to this attitude than would apply
in more theoretically motivated disciplines.

   A simple recapitulation of the history of  resistance of
microbiologists to the methodology and the cognitive framework of
genetic biology is that monomorphist doctrine, when strictly construed,
threw out the baby of bacterial genetics along with the dirty bathwater
of contamination.

  The critical early years of modern bacteriology 1860-1880
coincided with one of the most notorious of allegedly 'premature
discoveries': Mendel's seminal work on the delineation of genes as the
units of heredity. Undoubtedly, the new discipline of bacteriology
would inevitably have been profoundly affected if mendelism had become
established doctrine and part of the conceptual framework shared by
Pasteur, Cohn and Koch. With the notorious exception of Naegeli{ 15 )
and the problematical one of Beijerinck in the 1890's, there is hardly
any  evidence of mutual influence between Mendells neglected work and
the 19th century microbiologists.

   A more challenging problem in this intellectual history, not to
our knowledge investigated,  is the mutual influence of Darwin and
Pasteur. Darwin was aware that speciation in imperfect (asexual) fungi
would have to be analyzed separately from evolution in higher organisms
and could have contributed as a theorist to the debate over
polymorphism in bacteria. Darwin was also deeply interested in the
controversy over spontaneous generation { 16 ), and he and Pasteur
were surely aware of one another's principal findings and claims, if
only from the popular press. While Pasteur, for his part, made some
vague use of evolutionary ideas ,  the main recorded intersection of
their ideas in print  concerns the role of earthworms as agents of soil
turnover.

  By the time Mendel's laws were rediscovered in 1900 microbiology
was firmly established as a medical science of superordinate
importance. It was a specialized discipline already separated in the
educational schema from the studies of higher plants and animals. Its
mystique, connected with its concerns for infectious disease, imposed
particular experimental and cognitive approaches to these organisms,
one that,  as we have seen, relegated genetic variation of bacteria to
the category of nuisance to be avoided and ignored. Not until the early
1940's did bacterial variation again become an arena of critical
investigative inquiry in its own right - particularly with the work of
Luria and Delbruck on the spontaneity of mutations for resistance to
bacteriophage. But even the discussions of these years were marked by a
vicious cycle of intensified self-discouragement that went like this:
"Bacteria may have no genes, or at least they have no sexual processes
by which we could do the crosses to determine the laws of heredity
along Mendelian lines. Hence it is hardly profitable to study bacterial
mutations when we will be unable to draw clear analogies between the
phenomena of heritable change in bacteria and those of other

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organisms." But these mutational phenomena were the only tools by which
one could hope to examine the initial questions of genes in these
organisms!

   The doctrinal rigidity of Cohn's taxonomy notwithstanding, there
remained good reasons to assign bacteria a special status in the
hierarchy of living organisms. They were very small; they appeared to
comprise structures far simpler than those of other cells; they were
characteristically unpigmented and motile like animals; but like plants
they lived in solutions without eating solid particles. And at one time
one might even have believed that they were amenable to spontaneous
generation.  Once such a cluster of attributes becomes established in
scientists' imagery, it requires special provocation to try to splinter
away some of its elements.

  Particularly troublesome was the evident lack, until about 1935,
of an organized nucleus in bacteria, so far as the cytological methods
could tell. Even then,  the claims for the demonstration of
"nuclear bodies" with special stains -- including the DNA-specific
Feulgen reaction -- were unpersuasive until the development of electron
microscopy in the 1950's. At that,  these new methods showed that the
visions of mitosis asserted by some imaginative cytologists after 1946
were illusory. The DNA of the bacterial cell is typically organized
into a single tightly wound filament that obviates the later evolved
differentiation of separate chromosomes and a mitotic process that
would keep them in order. Consequently, the few geneticists who made
any effort to incorporate bacteria into a comparative system
(like Huxley and Darlington) reinforced the image of bacteria as
'missing links', organisms so primitive that they had not yet evolved
'differentiated genes'. This ideology gave strong support to workers
like Hinshelwood (v. infra) who then sought to use bacteria as
exemplars of pre-genie levels of organization for physico-chemical
analysis. Accordingly, bacteria might also be more immediately
responsive to their environment than higher organisms, whose genes had
been evolved (in part) to preserve the genetic autonomy of the
organism. Until the complexity of microbial biochemistry, its homology
to the metabolism of higher organisms,  and the universal role of DNA in
genetic systems were better understood, these speculations were at
least philosophically attractive.

   The biochemical analysis of microbial nutrition{ 17  ) was a major
impetus in the 1930's to the reexamination of the relationship of
bacteria to other forms of life. The discovery of the similarity in
chemical composition of bacteria to other forms; the idea that
differences in nutritional requirements were secondary to losses of
biosynthetic capability (that is, in some respects a bacterium is
biochemically more competent than a man!) was coupled with the
discovery of many specific enzymes that could be found both in bacteria
and in higher organisms. These homologies also inspired Beadle and
Tatum's work on Neurospora (1941), which showed the utility of a
microorganism,  in this case a fungus,  as research material for studies
in the genetics of metabolism. These studies made it possible to show
how genes influenced the development of the organism
through the encoding of specific enzymes, work that culminated in the
deciphering of the genetic code in the 1960's.

   This was also the time of renewed speculative interest in a
biochemical theory for the "Origin of Life:  Oparin's book of this
title become widely available in English translation in 1944; and
Schrodinger's (What is Life") likewise focussed attention on

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fundamental questions that demanded an integration of the biology of
viruses and microbes with the more traditional biology of plants and
animals.

   The mechanism of genetic variation, or mutation, was a fundamental
issue in all of these speculations; and here again mutation in bacteria
promised to be particularly important as an experimental measure, but
still blurred by manifest uncertainties whether, truly, "bacteria had
genes."

   Another movement of biological thought during this period was the
unification of Mendelism, quantitative population theory, and Darwinism
into a reformulation of the theory of biological evolution. Darlington,
around 1930, and later Ernst Mayr and Dobzhansky systematically
developed the idea of genetic systems of varying complexity, and
particularly the notion of species as mendelian breeding populations
or isolated gene pools.  The idea that sexuality itself was an evolved
genetic system was particularly provocative, with fascinating
illustrations in the life cycles of various orders of simple and more
complex plant life, from fungi and algae, through the mosses, ferns and
flowering plants. The concept of genetic isolation as the essential
condition for the differentiation of species, -- the observable product
of biological evolution --  certainly put renewed critical emphasis on
the biological significance of sexuality. Indeed, according to
neo-Darwinian theory every colony of an asexual biological form would
have to be  regarded as a distinct species, since by definition its
genetic content would represent a gene pool totally isolated from that
of every other. Dobzhansky's monograph,  "Genetics and the Origin of
Species" was widely read as the definitive reinterpretation of
Darwinian theory of evolution and reinspired intense interest in the
details of breeding systems as the key to the understanding of the
details of evolutionary development.

   The late 1930's and 1940's were then a time of renewed deep
interest in the evolutionary significance of sexuality. This sharpened
concerns about how to understand the evolution of organisms like
bacteria which were believed to be devoid of sexual mechanisms.
The neo-Darwinian model of random variation subjected to the creative
filter of natural selection was by now preeminent in the biology of
higher plants and animals.
However, as Luria remarked in his 1947 review, bacteriology remained
the last stronghold of the Lamarckist doctrine, e.g. in widely held
beliefs that the development of drug resistance among bacteria was a
hereditary change induced by the environment.{ 18 }

    The scientific discussion of this issue was complicated by its
Lysenkoist implications, at a time when the USSR had adopted an
official (and repressive) faith in the role of environment in changing
the hereditary character of crop plants and of Socialist man.
The side-effect of these political externalities in American
biology (we do not speak here of the social sciences) was as much to
provoke some intolerance of unconventional (i.e.  unMendelian) views as
to bias the  judgment on scientific matters of those who were
politically sympathetic to the Soviet view. So, on the one hand,
informed geneticists like JBS Haldane broke with the Party on this
issue, at the same time as innumerable left-inclined spectators from
other fields strained hard to find support for Lysenkoism in any
vaguely understood observation that looked like an environment-induced
adaptation in bacteria. Whatever other effects this sorry episode of a

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national-official science had, it was one more source  of focussed
interest on the mechanisms of genetic change in bacteria.

   The most carefully worked-out theoretical model for direct genetic
adaptation in bacteria was presented by Cyril Hinshelwood (a well
known physical chemist, and later Nobel Prize winner in that field) who
in 1946 published "The chemical Kinetics of the Bacterial Cell". This
was an intellectual tour de force in describing the bacterial cell as a
network of coupled chemical reactions but devoid of any specifically
differentiated genetic material.  It mobilized a vast amount of data in
defense of this model and in opposition to the idea of discrete
mutational changes in bacteria. As we now know it was existentially
totally inaccurate, owing to an  insufficient regard for the subtleties
of population dynamics of mixed bacterial cultures subjected to natural
selection (a subject that became the principal theme of F.J.Ryan's
research after 1946).

   Progressively deeper understanding of the life-cycles of other
unicellular organisms was certainly among the provocative stimuli for a
reexamination of bacteria. A 1941 symposium on the 'Genetics of
Pathogenic Microorganisms' exhibits an extraordinary contrast, within a
single volume, of the advanced status of genetic studies of fungi of
great economic importance, like rusts and smuts, and the mumbo-jumbo
that surrounded the discussions of bacterial variation. That such a
conjunction could occur at all was new.  It may have helped direct
Lederberg's interest to those mycological precedents for microbial life
cycles.  More immediately he recalls the paper by Beadle and Coonradt,
1944, on heterokaryons in Neurospora, and the emphasis that Beadle put
on them in his Harvey Lecture  (Feb. 1945) as evolutionary precursors
of sex. (Heterokaryons  are associations of different nuclei within a
common cytoplasm. The branched hyphae of fungi, often not completely
septated, lend them to such associations, which fall short of sexuality
by not going on to NUCLEAR fusion or fertilization.) Beadle's remark
that one could identify such heterokaryons by their nutritional
competence was also a forerunner of the selective method later applied
to the discovery of bacterial sex.

The turning point: DNA, Avery, the pneumococcus transformation.

The turning point of the story, however, was the discovery in 1944 by
Avery, MacLeod and McCarty that identified DNA as the transformation
principle which had been shown to change rough non-pathogenic
pneumococci into smooth virulent ones. The phenomenon of transformation
had been discovered by Griffith in 1928. Avery's skepticism was
surmounted by the work of Alloway, Dawson and Siu done in his
laboratory (according to Olby {20), almost surreptitiously in the face
of Avery's hostility.) Subsequently, Avery organized the team effort
that culminated in the 1944 report.

   In a recent characterization of the Rockefeller work as premature,
and thus comparing it to Mendel's long-neglected discovery, Stent { 19 }
has confused legitimate skepticism about the proper interpretation of
pneumococcus transformation with a lack of appreciation for its
significance for biological theory.  Lacking other means of
categorizing genes in bacteria, one could not be sure of the homology
of transformation in pneumococcus with genetic change in higher
organisms.  Furthermore, although the identification of the active
substance as DNA was a plausible, and in retrospect, the correct
chemical interpretation, this issue deserved the kind of skeptical

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challenge it elicited from Mirsky precisely because of its overarching
importance.

   As noted in Section II the Avery group report was the subject of
lively debate at Columbia, in view of its portent for the chemistry of
the gene, and was the immediate provocation for Lederberg's entry in
1945 into the field of microbial genetics.  It was also highlighted in
by Dubos { 10 }, as the avenue by which the chemistry of heredity might
be solved. These developments were the immediate context in which the
problem of bacterial sex was confronted in 1945. In a sharply focussed
critique of the status  of this problem, Dubos { 10 } wrote:

If bacteria do really reproduce by sexual methods, it should be
possible to cross closely related species and strains and to
determine something of their genetical behavior. Although there
have been isolated reports of successful crossing, most workers
who have attempted to cross related strains have reported only
failure. (Gowen and Lincoln 1942) ["Most" here refers to two
papers:  the one cited, and Sherman and Wing, 1937.1

In effect, the evidence presented to establish sexual reproduction
in bacteria is not convincing.  tp. 181)

Some sense of how things seemed earlier in the 30's is conveyed by
Sherman's perception of his own work. As Editor of the Journal of
Bacteriology, on receiving a manuscript from Tatum and Lederberg in
1947, he wrote:  "At the time [our 19371 work was done, variability in
bacteria was scarcely a respectable subject -- let alone ideas on sex!
However I have always thought that the approach used was a good one...

     He was,  it seems, one of the few occupied with the problem. C.F.
Niven, one of Sherman's students at Cornell, recalled how little
interested others were:

Sherman's interest in bacterial sexuality dates back to his
earlier days as a USDA bacteriologist,...During my eleven
years stay at Cornell,  Sherman's keen and intense desire to
either prove or to disprove the existence of bacterial sexuality
was evident almost on a daily basis. He repeatedly attempted
to encourage his graduate students, myself included, to pursue
further some of his earlier work, much of which was never published
because of its inconclusive nature.Many of us did have a go at some
of his ideas, but I'm afraid that our interests naively resided
elsewhere.. .We youngsters could not become believers, and
when Sherman expressed denial [of] bacterial sexuality, we
generally viewed his negativity in the sense of a denial from an
eager bride."
(Niven to Lederberg, 7 March 1974)

  Although Sherman was on the right track in the general design of
his crossing experiment,  which looked for recombination of markers for
sugar-fermentation, that design can be (retrospectively) faulted on two
grounds. It did not use a powerful method of selecting for recombinants
-- hence it would overlook any process that involved less than a few
per thousand cells. Furthermore,  the markers themselves were rather
unstable, so that their variation was too easily confused with the
outcome of possible recombination.

The major textbooks in microbiology and bacteriology  continued to

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assert the asexuality of bacteria. Moreover, microscopists had found no
persuasive morphological evidence of sexual reproduction in any
representatives of bacteria or in blue green algae. This was so even
though a rich variety of sexual processes had been observed in "higher"
microorganisms:  fungi and protozoa, starting with Leeuwenhoek's
original descriptions of copulating protozoa. These studies of sexual
process in non-bacterial microorganisms (eukaryotes) shaped
researchers' images of what such processes were like. Roger Stanier has
observed "[This] led to the establishment of a certain idea of the
nature of sexuality which.. ..made it very difficult to entertain the
possibility that bacteria might handle things differently.....Once
natural laws of  wide validity are established, there's a natural
tendency [sic] to treat them as universal". (Stanier to Lederberg, 2
February 1974).

   The adoption of E.  coli strain B as the 'standard research
organism' by the phage group in the earlier 1940s did a great deal to
strengthen the rigor and access to mutual criticism of work in that
field. But it also encouraged the universalist fallacy, and delayed the
recognition of important phenomena like bacterial sexuality and
lysogenicity for which, by unpredictable chance, that strain happened
to be ill-suited.

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IV. The growth of science:  cognitive and social factors

Continuity and Discontinuity in the Growth of Science

    Historians of science have often noted that the various sciences
are not equally well developed at a given time.  The more we already
know about a subject, the more new questions are raised, and more
further research is stimulated. Sectors of science, like the
reputations of individual scientists  thus appear to be subject to
cumulative and self-augmenting processes.{211

   All of this makes for considerable turbulence{22) in the advance of
different sectors of scientific knowledge,  which may be functional;
but it is difficult to see the mechanism by which the larger scale
aspects of the scientific process are necessarily adjusted to
optimize the cognitive goals of a system which has evolved in
response to many social, historical and accidental factors.

   Besides unevenness in the growth of divers fields, scientific
growth is also subject to temporal discontinuity: to prematurity and
what we have called post-maturity. Premature contributions are
neglected or overlooked at the time of discovery by the contemporary
community of scientists:  in retrospect they are viewed as having been
"ahead of their time".  Mendells discovery of particulate inheritance
in 1865, lost to view for thirty-five years, is perhaps the most
famous episode of prematurity.  Since premature discoveries are, by
definition, not incorporated into the body of knowledge at the time,
they do not form bridges to immediate future knowledge. They are
often insufficiently or unclearly connected to the immediate
scientific past or, as Gunther Stent has put it, to "canonical
knowledge".  (23) Still another formulation, this time in the Kuhnian
framework,  is that such discoveries are not consonant with the
prevailing paradigm  -- with dominant views about the central
challenges and methods of attack prevailing in the field. These are
not of course the only sources of prematurity in science. The
organization of scientific knowledge and activity into specialties
makes its own contribution.  As both origin and outcome of the
extension of scientific knowledge, specialization is in large measure
functional for the scientific enterprise.   But it is also
dysfunctional insofar as knowledge may become encapsulated within
disciplines and fragmented in specialties.  (24) Thus the cognitive
elements necessary for understanding new contributions may be present
in science at a given time but be
"misplaced": that is,  they may not be available in the domain in
which the contribution first appears.  That contribution, premature
in its own domain, is apt to be relegated to the archives or lost to
view altogether unless it is perceived and communicated across
specialty boundaries by researchers who have the perceptual set
required to understand it.  It has also been noted that obscurity,
either of the discoverer or his place of publication, and
incompatibility with prevailing religious or political doctrine have
been social structural barriers to the incorporation of scientific
ideas into ongoing scientific work and thus have contributed to their
neglect.

   That premature discoveries and resistance to what later proved
to have been authentic and significant contributions have social as
well as epistemological sources has been suggested by Barber, Merton
and Cole {25}.  Postmature discoveries by contrast have been noted now

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and again but neither the pattern of postmaturity nor its
problematics has been systematically discussed. In self-exemplifying
style, focus on the problem of post-maturity is itself postmature.

  The postmature contribution is a mirror image of the premature
one. Whereas the premature was made at an early time, but was not (or
could not be) understood by contemporaries, the postmature discovery
-- by retrospective judgment -- failed to be made at a time when it
was both technically achievable and could be understood and its
importance  appreciated. Characteristically, important discoveries
generate a wake of new questions and techniques, sometimes a
large infrastructure of information and further challenges to
falsification, which lead in turn to new discoveries. Why the first
pebble was not dropped may be the puzzle that raises the question of
"postmaturity", especially when far-reaching waves are eventually
generated.

This judgment of course implies a norm of homogeneous, successive,
and consistent development of scientific knowledge across a broad
front, perhaps constrained by the limitations of the current paradigm.

   Thus Linus Pauling reports that "there was no reason why" he
should not have discovered the alpha helix eleven years before he and
R.B. Corey actually did so.  {26} And C.N. Yang remarks that it is
"startling that parity conservation [one of the space-time symmetry
laws] was believed for so long without experimental evidence". {27)
Experimental cues that parity was not conserved were observed as
early as 1928 128) but the avowed law was not considered
problematical until 1955. Yang and T.D. Lee's discovery and
theoretical elaboration of parity nonconservation brought them the
Nobel Prize in physics just two years later.

  The two kinds of discontinuity in scientific development differ
in the kind of evidence used to ascertain them. Premature discoveries
are located in the domain of factual history; postmature discoveries
in the domain of counterfactual history. We identify premature
discoveries through the fact that they were rediscovered {29) later

--- postmature discoveries through the counterfact that they could
have been discovered earlier. (30) Premature discoveries are often
described as having been "neglected" and postmature ones can be
described as having been "delayed".  Such formulations smack of Whig
reinterpretation of history (31) but they serve quite the contrary
theoretical purpose. They provide convenient handles for grasping and
analyzing discontinuities in the growth of scientific knowledge and
help alert us to the difficulties of a model of undeviating progress
of scientific knowledge.

  The occurrence of postmature discoveries calls attention to the
fact that there is always a population of problems competing for the
attention of subsets of scientists {32}.  But, given limitations on
their time,  attention and resources, they can actually deal with only
a limited fraction of the problems  that may be apparent at a given
"stage of scientific development".

   Most of the time scientists continue work along lines similar to
those they had been working on earlier. Systematic evidence has yet
to be gathered on inertia in problem choice over the course of
scientific careers. However, scientists are apt to develop
increasingly great investments in expertise and knowledge in a given
area (equivalent to what the economists refer to sunk cost) and the
social system reinforces that inertia by imposing selective demands
and opportunities for remaining in that area.  Thus,  scientists are

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hired into slots to teach certain specialties while others in their
departments are not as qualified to do so as they are; they receive
information which will be selectively pertinent to their continuing
research interests and they are called upon to write or speak on
subjects others define as their areas of expertise.  Taken together,
the individual motivation to remain in a specialty area owing to
prior investment and the social reinforcement to do so probably
combine to produce something like "cumulative inertia" with respect
to problem choice. {33)

   Such limitations require choices among mutually exclusive
allocations of intellectual capital. Many discoveries will be
postmature for the good reason that alternative challenges were
deemed important, achievable and exciting at the time.
  Preemption seems to account for the delayed discovery of

Pauling's alpha helix. In 1937,  there was no great pressure to
explain x-ray diffraction photographs of alpha keratin and so, after
part of a summer's work and no success, Pauling found other problems
more engaging. Presumably the attention of other scientists at work
on neighboring problems also got diverted from the structure of
substances like alpha keratin. It turns out, in this case, that the
same scientist responsible for the postmature discovery could also
have made it earlier and testifies to knowing much earlier what
needed to be known to have done so. In most cases of such near
misses, however, the postmature discovery is made by others.

   Preemption of attention is only one of two broad generic
processes that appear to be involved in the occurrence of postmature
discoveries.  In cases of preemption,  scientists have identified the
problem but elect not to pursue it. In the second type, such
decisions are foreclosed because scientists do not perceive that a
problem exists. It is one thing to put a problem aside and another
not to know one was there in the first place. The fixity of
assumptions, beliefs and images most scientists must hold for the
organization of knowledge may serve as cognitive obstacles to their
perceiving what otherwise would have been clear lines of inquiry. In
the case we are about to examine,  convictions about the very
definition of bacteria were basic to the discovery's having been
delayed by some 45 years. Nomenclature and definitions, as we shall
see, affect the scope of scientific inquiry, what is taken as germane
and what is taken as trivial, and are perhaps the most profound and
consequential of assumption structures. Assumptions when taken as
fact, markedly decrease the chance that a matter will become
problematic and ultimately subject to falsification.{34) How this as
well as other cognitive and social elements delayed the discovery of
sexual recombination in bacteria is the next matter for examination.

  Cognitive and Social Processes in Problem Identification and
Selection

  Parity conservation and asexuality of bacteria are two examples
of scientific V1truths" unquestioned by most scientists for a long
time. How is it that such convictions are perpetuated and then later
transformed into questions worth investigating? Can we identify the
difficulties in and processes by which entrenched ideas are
transformed into problematic ones?

   The historical framework of the emergence of bacterial sexuality
as a scientific issue was summarized in section  < >. Here we may
reexamine some broader questions relating to the delay or
postmaturity of scientific discovery.

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   Technical difficulty leading to research failure is not
sufficient to explain the present example. Some investigative
failures, particularly those that are inexplicable, may stimulate new
research into the relevant methodology.  (Perhaps this can be said of
whole sciences!)  But failure which is readily attributable to "mere"
sloppiness is more likely to dampen new efforts and divert research
attention elsewhere. Few bacteriologists could have been motivated to
take up a problem which seemed to have  little intellectual merit and
substantial procedural difficulty.  Scientists manifestly distinguish
between reputable and disreputable error. Error of all kinds is to be
avoided, but it is one thing to be wrong in spite of having taken all
appropriate precautions; another to be misguided and inept. There
are,  as a consequence, strong incentives to avoid problems which are
"error prone", problems which in the past have acquired a reputation
for producing results which turned out to be irreproducible. All this
is reinforced by norms which prescribe caution when making claims
which  undermine prevailing views. These norms, rarely articulated by
scientists, protect active researchers from time-wasting diversions
and minimize the number of false reports enshrined in the archive.

   After repeated episodes of failure attributable to contamination
of samples, something like the process of reaction formation made the
further study of bacterial variation {35) aversive.  This apparently
psychological explanation of the foci of attention of individual
scientists has a social counterpart.  Scientists in the aggregate,
after all, share similar opinions about scientific problems; some are
considered promising, others are not; some are likely to yield
solutions easily, others with difficulty.   The collective focus of
attention in each science represents the sum of individual decisions
about what not to study (decisions affected by shared opinions), and
these decisions in their turn affect the subsequent reputation of
problems,  unless of course new solutions are found which alter
collective scientific opinion.  So much for why microbiologists might
have avoided the problem of bacterial variation.

   The fact was that many did not even see it as problematic. As we
have noted, bacteria were, by definition, asexual for the practical
purposes that evoked the characterization.  According to the great
classifier Ferdinand Cohn, they were fission fungi or schizomycetes.
As such, they did not reproduce by means other than fission.   Since
sexual recombination could not occur in bacteria and since the same
organism did not change its form during its lifetime, monomorphism
became the rule of the day.  It thus becomes clear that the labelling
of scientific phenomena has consequences for the way that scientists
think about phenomena much as social labels are said to be socially
consequential definitions of  those who are labelled. {36)
   By reorienting the scientist's perception, labels   influence the
choice of problems, and may delay the reexamination of fallacious
traditions of misplaced concreteness or precision.  They come to be
self-fulfilling prophecies {37).  Consider the impact of the terms
atom, ether and noble gas on scientists' conceptions of matter. For
centuries,  atoms were indivisible;  and ether was the substance which
filled space.  Noble gases were inert or unable to form compounds. By
reinforcing the security of current theory and encouraging further
exploration, labels tend to outlive the rational arguments on which
they were based. They are one of the principle mediators of rigidity
in collective memory and intelligence.  This is not to deny the
constructive function of labels for scientific development
(obviously they are required for abstract thinking) or even that

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labels always dampen scientists' skepticism about the traditional
images. Explicitly dogmatic labels may have quite the opposite effect
in stimulating scientists to challenge the received word, as it seems
to have for Neil Bartlett who demonstrated that noble gases were not
inert and could indeed form compounds. Labels carrying less explicit
dogmatic freight than, say,
"noble gas" may restrict scientists' thinking most of all. Systematic
analysis of the effects of labels on scientific development  should
enhance what we know about the classical sociological problem of the
social effects of definitions of the situation in science.

  Disciplinary structure and the investigation of bacterial
sexuality.

  Disciplinary structure also exerted its own effects on
bacteriologists who might have examined the problem of bacterial
sexuality. By the later part of the nineteenth century,
bacteriologists were principally concerned with bacteria as
pathogenic organisms and the means of eradicating them. Members of
the French, German and Austrian schools were oriented to the
(enormous) practical medical implications of their work. The notion
that bacteria deserved equal  attention as strategic targets of
fundamental science was for some time the special province of a small
group of Dutch scientists known as the Delft School.

  Proudly evoking their descent from Leeuwenhoek, the Delft School
of bacteriology clearly separated themselves from the medical
bacteriologists who maligned bacteria.  Martinus Beijerinck, who
independently discovered the tobacco mosaic virus and was the
principal figure in this group was at odds with prevailing dogma
about the invariability of bacteria.  He was prompt to cite the
importance of DeVries new findings on mutation in plants, and offered
some of the first and most coherent challenges to strict
monomorphism. {39) He also relied on "enrichment culture" methods,
which were an early forerunner of the selective techniques
successfully applied later  in the discovery of bacterial
recombination. He was personally involved in  the rediscovery of
Mendel's work {40}.  He thus was far better informed than most of his
contemporary microbiologists about the new work on plant
hybridization and mutation that would have been instrumental in
planning an investigation of sex in bacteria and understanding the
observations. Lederberg finds it surprising that Beijerinck did not
discover bacterial recombination in the first decade or so of this
century.But in fact he strongly reechoed the Cohnian dogma of
Schizomycetes.

  Nevertheless, Beijerinck, A.J. Kluyver, and C.B. vanNie1 had an
important indirect influence through their espousal of comparative
biochemistry  as an approach to the understanding of evolution and of
fundamental cellular processes.

  Although Beijerinck and other members of the Delft school were
likely candidates for making the discovery of bacterial sex, students
of genetics were not. Geneticists were occupied with larger organisms
in which the products of crossing (the bases for studies of heredity)
were easier to observe. Bacteria are very small and were then almost
impossible to work with cytologically -- and besides, following Cohn
and the bacteriologists, they were believed, even defined not to have
sex. Thus the problem of sexual recombination fell between

Jan 29,  1998 1:55pm

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disciplinary stools, finding a place neither in bacteriology nor in
genetics. As long as the monomorphic view prevailed in bacteriology
and as long as there appeared to be no urgent motive for
bacteriologists or geneticists to want to know whether bacteria
reproduced sexually, the subject would remain an unacknowledged and
long-gestating bastard.

   Although the Delft school was the major deviant from the
strictly medical orientation of bacteriological study in 1900, by
1925 a considerable fraction of the published research was conducted
by Ph.D.'s, many of whom had been trained originally as chemists or
biologists.  In a crude effort to assess the disciplinary rigidity of
bacteriology, we examined the biographies of American authors of
papers published in two leading journals. In 1925, less   than a
fourth of the 49 identifiable authors of papers in the Journal of
Infectious Diseases and only half of the 44 in the Journal of
Bacteriology were MD's. Contrary to a more naive view of the frame of
the discipline that we had previously entertained, plainly MDs did
not dominate the literature at that time nor were strictly medical
issues of paramount concern.

   The gap between genetics  and medical bacteriology might better
be characterized as a barrier between fundamental and applied
science.  This gap appears to be endemic -- turning up as it does in
many areas of physics and engineering as well as in the biological
sciences and  medicine and seems a likely source of lost
opportunities for systematization of knowledge. {41) While there is
no inherent conflict between theory and practice, examples of their
convergence -- as for example Wiener's cybernetics or Claude
Shannon's work in communications -- are remarkably few. The sporadic
communication between scientists and practitioners is reflected in
the tenuous linkages of their published writings, which has led Derek
Price to proclaim that science and technology develop essentially
independently of one another.  {42) Be that as it may, the hindered
interaction of  science and relevant applications is apt to create
discontinuities in knowledge on both sides.

   So far, our discussion of the discovery of bacterial
recombination has focussed on discontinuities in scientific
development and some of its sources.  Now we turn to a separate but
not altogether unrelated question.  What can be learned about the
impact of the social contexts of science by examining the present
case,  the scientists's social origins,  the educational system in
which he was trained, the institutional contexts in which his
specific research interests developed and some specific features of
the discovery of bacterial recombination?
   Lederberg was, as he noted, the son of a Rabbi, raised and
educated in New York City in the 1930's. The best data on hand on
the religious origins of American scientists show that Jews are
statistically over-represented in the professoriate, especially in
recent decades. They now comprise about 10 percent of all professors
in the physical and biological sciences as compared to the general
population figure of about 3-5 percent.
   Even in the light of this predisposition, the differentiation of
Lederberg's scientific interests occurred at a very early age, as can
be documented, e.g., by a letter from one of his teachers. She writes
of the twelve-year old Lederberg:
   Early in 1937 . . .  I had a most unusual
   pupil whom I still remember vividly. I can still remember how
   he prepared a paper on the classification of Protozoa.... using

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a graduate text for a reference.....It is more
than just possible that I am guilty of being the first one to
teach you that bacteria divide only by simple fission.
(Mrs. Fanny S. Rippere 2/24/59;  3/10/59)

In addition to its conventional academic and commercial high schools,
New York had several elite schools which were open only by
competitive examination. Stuyvesant High School and later Bronx High
School of Science, unlike Boston's Latin School, emphasized science
and mathematics and brought substantial numbers of bright boys
together with able teachers in a comparatively demanding and advanced
science curriculum. Bright girls could attend Hunter High School
which put a premium on preparing its students for the liberal arts
colleges but not for the sciences per se.    Lederberg's scientific
indoctrination was augmented by attending the American Institute
Science Laboratory.  In the 1930's, New York's cosmopolitan atmosphere
offered great opportunities of all kinds to motivated youngsters.

   Data on men and women in Who's Who (1976-77) are consistent with
this assertion (25).  About 13 percent are native-born New Yorkers
while the City has had slightly more than 5 percent of the nation's
population since the turn of the century (26). But an even greater
share of American scientists come from New York City. Twenty percent
of the physical and biological scientists in American Men and Women
of Science who were American-born, list their birthplace as New York
City (27).However,  until detailed information is available on the
religious and geographical origins of American  scientists, it will
not be clear whether New Yorkers are overrepresented among Jewish
scientists generally or particularly among those of Nobel prize
caliber.

   Lederberg was 16 years old when he graduated from high school.
Columbia University and the towers of its Medical Center ( near his
home) symbolized the wide world of learning and first class-science
for him. But it seemed then that he had little choice but to go on to
the City College of New York in the light of the Lederberg
household's finances. (48) Even though it seemed out of reach,
Lederberg applied to Columbia nonetheless. He was awarded a tuition
scholarship just large enough to allow him to attend that fall.

   He sized up the opportunities then available on Morningside
Heights,  decided that he was unenthusiastic about classical
Mendel-Morgan genetics and elected to spend most of his time on
cytochemistry and physiological embryology. If these seem highly
specific interests for a 16-year-old, they were nonetheless consistent
with his self-defined research program of "understanding the chemical
nature of life".

   Dobzhansky had just arrived from Cal. Tech. He and others at
Columbia,  such as Alfred Pollister were well integrated into the New
York scientific communication network which kept them in close touch
with work at the nearby Rockefeller Institute where Avery, Dubos and
Rous worked.  Pollister's collaborator, Mirsky, in fact shuttled
between the two institutions.

  When Lederberg was a sophomore, he met Francis Ryan, as he
recounted earlier. Ryan, "adopted" Lederberg and found work for him
as a laboratory assistant.  It was from Ryan that Lederberg first
heard about the new biochemical genetics of Neurospora. And it was
Ryan who persuaded Lederberg that chemistry and genetics need not be
so far removed from one another as Lederberg had thought.

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   In short, Columbia provided as much informal access to the
research front in biology as any other American university at the
time.

   Quantitative studies of the impact of college environments on
the production of future scientists show weak
"school effects" in comparison to the much stronger effects of
"inputs"  or student abilities.  These studies understandably have not
focussed on detecting effects of particular collegiate environments
and particular teachers  nor on differential outcomes in specialized
disciplines; whether, for example,  the University of Chicago in the
postworld War II period was especially productive of nuclear
physicists or Cal Tech of the 1950's, of molecular biologists.{49)
   These general findings aside,  Columbia College did offer a
number of specific opportunities to Lederberg. He was strategically
located in an information network which encompassed the various
strands of biology described earlier.  It offered the opportunity to
be adopted by a Ryan who would nurture his interest in research. It
was also fortunate for Lederberg that Ryan was not yet so well
established as to be already preoccupied with training many graduate
students who would have prior claims on his time. On the other side,
Lederberg's precocity facilitated his use of an advantageous social
structural location in ways that other students with more
conventional assets could not.

   Although he was an assiduous bibliographer, covering and
digesting vast sectors of the biological and chemical literature on
his own, had he gone to City College, he would not have been privy
to first-hand reports of the Beadle and Tatum work, would not have
learned the details of selective bacterial nutrition, would not have
had the opportunity to work with Ryan and might not have heard of the
Avery work until some time after in fact he did.

   Six months later, in July 1945, he had written in his laboratory
notebook that sexual recombination in bacteria was a meritorious
problem that could be attacked with the methods related to the
Neurospora work. He and Ryan had just completed a paper (50) --
Lederberg's first publication -- on reverse mutation in Neurospora
which used the technique of marking mutants by their nutritional
requirements. First hand experience with this technique of
nutritional selection led directly to insight how to detect sexual
recombination in bacteria.

    The opportunity to study at Columbia thus offered access to a
communication network, a research milieu,  and the tutorship of an
energetic but generous and considerate Ryan, which facilitated both
his perception of an important problem and the technical skills to
attack it. Ryan's place in the invisible college that now connected
Stanford, Columbia and Yale was also instrumental in his introducing
Lederberg to Tatum, and in arranging the funding of an unusual
fellowship at a time before the National Institutes of Health had
invigorated biological research in this country.

   Being strategically located in this environment was however not
determinate. After all,  there were others there who did not think the
question of sex in bacteria was problematic and who spent no effort
to devise a method whereby it could be decisively observed.
Lederberg's own brand of skepticism (which he thinks every autodidact
must acquire or be hopelessly misled) combined with his facility for
devising simple and effective research techniques were idiosyncratic.
But his structural situation at Columbia obviously offered many
opportunities for the growth and exercise of his particular abilities

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that might readily have been thwarted at other times and places.

   Although it was not evident at the time how Lederberg would get
leave to work in Tatum's laboratory -- medical schools' schedules
being generally demanding and inflexible -- the fact that Lederberg
was a medical student was less of an obstacle to his doing research
on bacterial sex than it might immediately seem. Since he was not a
regular graduate student obligated to do research for a formal
dissertation, he was not subject to the constraints that usually
apply at that stage of the scientific career. And this is a crucial
point:  unlike others who had to work on a problem with a predictable
outcome, Lederberg could better afford to take on a high risk problem
without much anxiety that negative results would stall him at the
very start of his career.

   The search for bacterial sex belongs to a particular class of
scientific investigations which made it high risk. It was a voyage of
discovery more than the cultivation of known ground. Not finding
bacterial recombination would not demonstrate it did not exist.
(It should be remembered that two earlier studies had been
unsuccessful).  Thus all of the effort involved in the experiment
might readily have been wasted since the reward-system of   science
provides few kudos for those who produce negative findings. (As it
turned out, the risk of a negative finding with the chosen species of
bacterium could be measured precisely. It was later found that the
phenomenon could be observed in just 5% of all strains of E. coli in
the way that it was demonstrated in K-12,  the strain that by lucky
chance had been chosen.)

   The experiment was high risk in another respect. The chances of
achieving contaminated and thus artifactual results were still great.
They had after all been documented for decades. But if the experiment
was high risk in the sense of not guaranteeing reportable results it
was clearly high yield by the measure of the significance of positive
findings.  Tatum by comparison to Lederberg already had his own
laboratory {51) and a variety of projects in process. He could afford
to include a long-shot experiment among them - especially if it was
not expensive.  The opportunity structure for investing in high
flyers is stratified and favors those with some situational  capital
{52} or -- as in Lederberg's case (he still intended to become an
M.D.) are deviant enough to be operating in another market system
altogether.  Therefore advantage appears to accumulate with respect to
winning on high risk problems just as it does in the social realm of
science. {53) Risk-taking is apparently not only a matter of
psychological daring but one of position in the social structure as
well.

   Further development of the notions of risk-taking in problem
selection in science and of problem portfolios containing items which
carry variable risk would of course benefit from intensive review of
the pertinent literature in economics and decision-making. By way of
example, elementary utility theory posits that risk-estimation
involves the probability of success, the cost of failure, and the
marginal returns and their utility of different kinds of investment.
Bacterial recombination for Tatum and Lederberg was a good gamble in
the sense that failure would have low marginal disutility (though for
different reasons for each of them), but promised large if
prospectively unlikely returns.

   It was clear that if Tatum and Lederberg were to be successful,
the discovery would be a very important one indeed. How is it that
Lederberg seemed unconcerned about revealing the details of his

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research design and how is it that Tatum, who himself was
contemplating a similar effort, agreed to have Lederberg come to work
in his laboratory and share his almost unique collection of
nutritional mutants? What can be learned about competition for
priority and secrecy in science from this case?

   Since publication in 1957 of Merton's study of competition in
science using priority disputes as a strategic research site,
competition for recognition of contribution has played a central role
in sociological thinking about the behavior of scientists. Merton's
analysis,  extended since, focusses on the abiding concern in science
with originality,  its functions for the advancement of scientific
knowledge and its role in producing competition, secretiveness,
priority fights, and, on rare occasion, outright fraud. {54}

   But secretiveness and competition, Merton holds, are contained
to a degree by an institutional imperative to share one's work and,
by extension, one's expert knowledge and research materials. {55)
Secretiveness and competition are also contained by pragmatic
considerations; isolation, after all, reduces access to information,
and critical corrective feedback and , at a social level can directly
interfere with gaining recognition. It also, as Hagstrom notes, takes
much of  the fun out of doing science. {56}
   The double emphasis in science on originality and open

communication can lead individual scientists to experience
considerable stress in deciding whether or not to share their ideas
with others before those ideas are publicly earmarked as their own.
No such stress can be perceived in the Lederberg-Tatum relationship,
either in Lederberg's memory or from anay available documents.

   Lederberg claims that he was not naive about the existence of
competition and plagiary in science. However,  in the light of Tatum's
reputation for scrupulous fair dealing with younger associates,
communicated via his close friend Ryan, Lederberg never entertained
the possibility that Tatum could plagiarize the research design
communicated in the letter. In any case,  the competitive world of
molecular genetics described by J.D. Watson in The Double Helix {57)
just a few years later does not resemble the environment in which
Lederberg began his career. Besides the possible role of personal
idiosyncrasy in creating differences in the tone of mutual
cooperation and openness, scientific fields vary in the extent to
which an idea is a purloinable quantum in itself, or needs additional
theoretical insights and technical skills before it can be exploited
for personal recognition.

   Empirical data are sketchy on the extent of competition in the
sciences. The most comprehensive are confined to scientists' reports
of the frequency their research has been anticipated by others. (58)
But this is just one aspect of the general process of competition in
science and is less germane to this discussion than the studies of
scientists' attitudes about open discussion of their work before
publication. Diverse and comparatively large samples of physical and
and biological scientists  report little anxiety about discussing
their research with others. Almost half report feeling free to
discuss their work with anyone.  And an additional two-fifths or so
report feeling free to discuss their work with most others. Most
scientists apparently are willing to communicate their   ideas to
almost anyone and if they feel uncomfortable about it, they do not
say so.{591  Lederberg's lack of concern about describing his
research plans in detail to Tatum was probably fairly typical of

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scientists at work at the time.

   But Watson's Hobbesian perspective on science is not altogether
deviant and inexplicable. Hagstrom and Sullivan confirming Merton's
early hypothesis, observe that competitiveness and secretiveness are
most characteristic of scientists who suffer from status insecurity.
(601.

   Much more work will be required to establish the diversity of
competitive behaviors exhibited in the various specialties as well
as within and between scientific schools.  Competition within a school
may well be restrained by a founder who systematically allocates
problems for investigation.  The Delbruck festschrift documents
several examples of his role in distributing problems among members
of the "phage group". {61).
   Finally, we turn to some of the effects of organized skepticism,
the institutional requirement that scientists critically scrutinize
each  new contribution even those they believe are correct. {62}
Lederberg has already recounted his debate with Lwoff and, in
passing,  on the further elaboration of work on the mechanisms of
bacterial sex.
    Here, we want only to touch upon the Cold Spring Harbor
presentation and to mention one instructive episode in the exercise
of organized skepticism. The episode in point involves vigorous
resistance by Mirsky against the Avery, Macleod and McCarty
conclusion that DNA was  the transforming substance. The claim that
no protein was involved in genetic transfer countered the widely held
belief that a protein was the most likely candidate for being the
hereditary substance. Nucleic acid molecules, as described by organic
chemists at that time, were considered far too simple to carry the
complex information of heredity.

   This episode is instructive for our purpose not because it
involved the major reformulation of Avery's work but rather because
it did not -- it was criticism that proved ultimately to be
unfounded. Exhibiting behavior strictly in conformity with the norms,
Mirsky was skeptical of the conclusion that Avery and his colleagues
had decisively ruled out the possibility that a protein might be
present in the purified transforming agent. {63}
   As it turns out, Rollin Hotchkiss, working in Avery's
laboratory, was also concerned that traces of active protein might
account for transformation. As he put it,
   My respect for proteins owed very much to long hours of
   fascinating learning from Alfred Mirsky... Quite on my own,
   then,  I felt the same doubts he did..... Mirsky spoke about these
   objections, but not very much to Avery's group or he would have
   learned as I did how eager they were to see the search for traces
   continued. (64) On both sides then skepticism prevailed.
Hotchkiss himself took on the job of doing the required experiments
which made it increasingly implausible that the genetically active
nucleoprotein was cofractionated with DNA. Avery's work was thereby
solidified, as it would not have been if doubts about protein had
been ignored.

   Conformity to the norm of organized skepticism, irrespective of
any ethical value it might have contributes to the advancement of
scientific knowledge.  It improves the chance that error will be
uncovered, and perhaps equally important,  it also strengthens valid
contributions by reducing residual uncertainty about them.
   The impact of organized skepticism can also be observed in the
records of the Cold Spring Harbor Symposium and in response to the

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three papers by Lederberg and Tatum announcing the discovery. The
first paper, published as a terse 497 word piece in Nature, October
1946, was not the first presentation of the work but reflected
earlier discussion at Cold Spring Harbor. Even as discoveries enter
the archive of science, they are not unitary events limited precisely
to what the contributors first proposed. Discovery is a complex
on-going process elaborated by criticism and by the contributors'
response to it.

   Treating discovery as a process makes it possible to identify
the fine-structure of the operation of organized skepticism -- how
contributors anticipate criticism, what arrangements are made for
public expression of criticism, what the range is of styles of
critical role performance, which kinds of scientists require which
kinds of evidence to become convinced of the validity of the work,
and finally, how the ultimate significance of the work is assessed.
1651

  The process of discovery takes in events not only in the
laboratory or in front of the blackboard but also those involving
response and counterresponse afterward. What we really mean by
designating this or that scientist as the discoverer is then
problematical. This calls into question the current practice of
sociologists of science of gauging the impact of a scientist's work
by counting citations to his name alone. Citation counts to the
authors of  originating papers probably underestimate the actual
response to the work associated with them. Such counts seem to
reflect a rather atomistic conception of the development of science
since they neglect altogether contributions surrounding the original
papers. New procedures of co-citation analysis now being used for
other purposes may be a way of reconstructing the complex of
published works that comprise a given contribution. (66)

V. Some conclusions and lessons

  If historical analysis is to go beyond the selection of
narrative detail and display some theoretical assertiveness, it ought
to be asked
"what if?": that is to make a plausible case for postdicting
alternative outcomes, given different hypothetical inputs.
  Quite possibly genetic recombination in E. coli as we know it

and describe as sexuality, might have remained undiscovered until
this day.  Furthermore, we could ask, only partly tongue-in-cheek, how
much regret that would entail. There is no question  that there was
already an irresistible impetus for the development of bacteria as
tools for genetic investigation. Without these findings about sex in
E. coli, there would nevertheless have been an enormous productivity
and possibly an even sharper focus of work in the tradition of the
Delbruck school. They had already discovered recombination in viruses
and the discovery of sex in E. coli was not a prerequisite for the
work of Hershey and Chase on the role of DNA in the virus life cycle,
or that of the other virus chemists. Without the distractions of
another genetic system like E. coli, even more attention might have
been paid to the pneumoccocal transformation or other systems like
it. There would have been a significant impediment from the lack of
very detailed genetic maps of the bacterial chromosome but they might
well have been built up piecemeal by other methods and partly by
analogy with recombination in viruses. Perhaps even more likely there

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would have been less emphasis on bacterial genetics and more on the
viruses with their simpler structure.  It is conceivable that this
would have led to even deeper and more rapid advances at the strictly
molecular level, perhaps at the price of a much vaguer picture of the
natural history of bacteria.

   What might have been bypassed could include some aspects of
phenomena like lysogenicity -- the incorporation of viruses into the
bacterial chromosome -- but other branches would have inspired
considerable work in that direction. So,  the minimum that can be
foreseen is that  other parallel channels of development in the
general area of molecular genetics might have been pursued even more
deeply; or alternatively that some completely different one, unknown
to us at the present time, would have emerged -- one that is now
neglected owing to the attractiveness of the E. coli system.

. . . . . .

   A variety of processes, social and cognitive, made the discovery
of sexual recombination in bacteria a postmature contribution and
thus delayed the development of the specialty of bacterial genetics:

   (1) The definition of bacteria as asexual -- symbolized in their
classification and denotation as schizomycetes -- diverted
investigators from looking for and observing sexual recombination;

   (2) Repeated experimental failure to demonstrate gene exchange
in bacteria and the fact that these experiments were susceptible to
contamination gave them the image of being risky and vulnerable to
disreputable error;

   (3) the movement in bacteriology to downgrade fundamental
research on these organisms in favor of the more practical and
socially rewarding studies in medical bacteriology. Thus the problem
had no appropriate disciplinary home.

   Using the vehicle of a detailed case study for analysis of
cognitive  and social processes in scientific discovery, we note that
problem selection in science has at least three features deserving
further analysis. First,  some good problems are preempted and may
eventually become postmature. Second,  in calculating the returns on
selecting one problem rather than another,  the probability of making
errors -- reputable and disreputable, is taken into account and
contributes to the continuing neglect of problems that have a history
of being error-prone. And third, the opportunity for taking on high
risk problems in science is unevenly distributed. Such problems are
typically left to the well-established who can afford to include them
in their more comprehensive research programs and to the small number
of others whose primary commitments are to a different system. This
uneven distribution of opportunities makes for accumulation of
advantage in the cognitive realm and in the social stratification of
science since major advances often can be made only by assuming high
risks.

   Thus we suggest that problem identification and selection
involves the interaction of cognitive and social elements in
individual investigators'  choices of what to work on and in the
resulting collective foci of attention in the sciences. What is taken
as problematic and worthy of investigation are the net product of
these interactions.

   The further study of such interactions in different fields
requires information,  sensitivity and expertise on both sides of a
kind that is most likely to come from interdisciplinary
collaborations.*

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* dedicated to the memory of Francis J. Ryan, Edward L. Tatum, and
Harriett Ephrussi-Taylor.

   Work on this paper began at the Center for Advanced Study in
Behavioral Sciences with support from the National Science
Foundation. [Program on Science,  Technology and Society at the
Center.] Our work has benefitted greatly by repeated discussion with
Robert K. Merton: his contributions should be evident throughout.
Yehuda Elkana,  also a fellow at the Center, helped to criticize early
drafts of the paper.  The junior author has been supported by the
National Science Foundation's grant to the Columbia University
Program in the Sociology of Science.

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Footnotes 1.  A longer account of Tatum's scientific biography is
forthcoming in the Biographical Memoir series of the National Academy
of Sciences. Memoirs on Taylor and on Ryan have appeared in Genetics,
60: 524, 1968 and ibid., 84: l-25, 1976.

2.    Saul Benison, Tom Rivers:  reflections on a life in medicine and
science. Cambridge: MIT Press, 1967.
   Wiener, Charles . . . to be furnished American Institute of Physics;
project on the recent history of physics interviews
   Thomas Kuhn, History of Quantum Physics. American Philosophical
Society. [ref ??I
   Nevins, Allan.  Re Oral History ??? to be furnished

3.  Space does not permit us to reproduce all relevant documentation.
Where assertions are based on unsubstantiated recollections, this
should be clear from the text.

4.  Woolgar, S.W. 1976 Writing an intellectual history of scientific
development. The use of discovery accounts. Soc.Stud.Sci. 6(Sept):
395-422.

5.   David R.  Zimmerman  Rh: The Intimate History of a Disease and its
Conquest. N.Y. MacMillan 1973, p. xv.

6.  Thus we had tacitly agreed that the scientistic eschatology
fulfills a Jewish interpretation of the Fall of Man.

7.     In retrospect, not a bad choice for a perspective on the
chemical basis of life. This work, published 1933, was unusual, for
example, in its detailed treatment of Garrod's work on "Inborn Errors
of Metabolism", which Beadle and others were to characterize as lost
genius a decade later.

8.  (For an account of the wartime officer-preparation training
programs,  and the contrast in Army vs. Navy administrations that made
this a fortunate choice, see Herge (1948)
  Herge,Henry C. Wartime College Training Programs of the
  Armed Services. Amer. Council Educ., Washington, 1948 See also:
Medical Training in World War II, Medical Dept.,
    u.s.Army   1974.

9.    For a discussion of some reasons why this perception may have
been so much more emphatic at Columbia than has been recorded by the
chronicler of the invisible college of the phage group, Gunther Stent
1231   see section IV.

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10.     It is not certain whether this work was available just before
or just after these questions were raised with Ryan. In any event it
was a treasure chest  of critically digested data on the biology of
bacteriology  that put the previous history in sharp, critical
perspective and furnished many ideas for new experiments.

11. more precisely by Kruis and Satava 1918, in work that had been
published only in Czech, and rediscovered, independently, by Winge

12.   Tatum,  1945 Proc. Nat. Acad. Sci. U.S., 31:215-219. ;
     Gray,C.H.  and Tatum,E.L., 1944. ib., 30:404-410.

13. Robert K. Merton, 1942 in 1973 The Sociology of Science, Chicago:
   University of Chicago Press, Ch. 13.
   B. Barber,  Science and the Social Order. N.Y.: Free Press 1952
    A. Cournand and H.A.Zuckerman The Code of Science. Studium Generale
       23 (Oct. 70) 941-962.

14.     Many intellectual as well as political revolutions suffer in
the long run from this kind of rigidification of defenses against
errors that had provoked them in the first place. Thus they sow the
seeds of their own obsolescence.

15.  one of the most influential advocates of bacterial polymorphism:
he is perhaps best known as one of Mendells few scientific
correspondents, and for having failed to  understand and thereby
discouraging the further dissemination of the friar's discovery.

16. According to H.E. Gruber 1974 , Darwin on Man. N.Y.: Dutton,
he anticipated some arguments of Oparin that the "first
primordial living things consume the complex but non-living molecules
from which they evolve, so that once done, the deed becomes forever
impossible".   p.152

17.  especially the work of B.C.J.G.  Knight and Andre Lwoff, reviewed
i.a., by Dubos ( 10 ).  These efforts at  a unified system of nutrition
owed a great deal to the concepts of comparative biochemistry in energy
metabolism that can be attributed to Albert J. Kluyver in Delft.

18. It would be fairer to say that most bacteriologists did not admit
of a distinction between hereditary potentiality and manifest phenotype
that would make this a well-formed proposition.

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19. See especially Francois Jacob,  1965, Genetique de la cellule
bacterienne. Les Prix Nobel en 1965. E. Wollman and F. Jacob, 1959 La
sexualite des batteries. Paris:Masson. W. Hayes 1969 The genetics of
bacteria and their viruses. New York:Wiley. and J. Lederberg, 1959 A
view of genetics. Les Prix Nobel en 1958, for reviews and
retrospections. The prehistory is well covered by Dubos { 10 }   and
Olby { 20 }. Current work on E. coli K-12 is  reviewed periodically in
Annual Review of Genetics, Annual Review  of Bacteriology and
Bacteriological Reviews.

20.    R. Olby,1975 The Path to the Double Helix  Seattle:U.
Washington Press.

21. Robert K. Merton, The Sociology of Science. Chicago; University of
Chicago Press, 1973. Ch. 20, originally published 1968.

22. In the hydrodynamic sense of self-sustaining vortices.
This follows the usage of
Millionshikov,  "The Place of Value in the World of Facts," Nobel
Symposium XIV. Stockholm: 1969.

23. Gunther S. Stent, "Prematurity and uniqueness in scientific
discovery," Scientific American 227 (December 1972) 84-93. Stent claims
that the Avery group's discovery of DNA transformation was premature
but there is ample evidence that the work was widely known soon after
it appeared, that it excited the imagination of many scientists, and
that it was the subject of numerous inquiries between 1944 and 1953.
See Robert C. Olby,
"Path..."; Dubos 1976, The Professor,  the Institute and DNA. New York:
Rockefeller Press; J.S. Fruton 1972, Molecules and Life. New
York:Wiley. J.S. Cohen and F.H. Portugal 1975, A comment on historical
analysis in biochemistry. Perspec. Biol. Med. 18(2):204-207; H.V. Wyatt
1975, Knowledge and prematurity:  the journey from transformation to
DNA. ibid, 149-156. Be that as it may, Wyatt's and Stent's general
views on the character of prematurity in science are well taken and
applicable to Mendel and other more apt historical cases.

24. On communication barriers in science, see A.J. Meadows, "Diffusion
of information across the sciences," Interdisciplinary Science Reviews 1
(1976) 259-267.

25. Bernard Barber, "Resistance by scientists to scientific discovery,"
Science 134 (September 1961) 596-602; Merton, Sociology of Science,
Chaps.  16 and 17; Stephen Cole,  "Professional Standing and the
reception of scientific discoveries, II American Journal of Sociology 76
(September 1970) 286-306. Among those who think that premature
discoveries do not exist because cognitive factors cannot be separated
from their intellectual context, see Yehuda Elkana, "The conservation
of energy: A case of simultaneous discovery?," Archives
Internationales d'Histoire des Sciences 23 (January-June 1970 31-60.

26. Linus Pauling,  "The molecular basis of biological specificity,"
Nature 248 (26 April 1974) 769-771.

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27. B. Yang, "The law of parity conservation and other symmetry laws of
physics," Les Prix Nobel en 1957. Stockholm: Imprimerie Royale, P.A.
Norstedt & Soner, 1958. Pp. 95-105, at p. 100.

28. After Yang and Lee had done their own work on parity
nonconservation, they learned of experiments done in 1928 by R.T. Cox,
C.G. McIlwraith and B. Kurrelmeyer which showed parity nonconserving
effects. Jeremy Bernstein observed that "at this time the study of weak
interactions was in its infancy, and there was just no theoretical
context in which to put the results. In fact, it was only in 1927
that... Eugene Wigner...  devised the first real mathematical
formulation of parity symmetry in quantum theory. Therefore it was not
as if the results had challenged an existing theory that was well
understood. They were rather a kind of statement made in a void."
"Profiles: A question of parity," New Yorker 38
(12 May 1962) 49ff, at p. 93.

29. Rediscovery of the phenomenon and the prior report almost always
occurs in that order.

30. A given lineage may include both. Many "lost" discoveries may exist
that had been premature and not yet reencountered and more late ones
where new knowledge is developed in substantial lag behind the
potentialities of the existing paradigm although no evidence but
experience exists for either type before the fact. The surprise
expressed by scientists that postmature discoveries were not made
sooner seems to derive from their usually unarticulated belief that the
cognitive ingredients of the discovery had been available for some time.

31. Herbert Butterfield, The Whig Interpretation of History. New York:
Scribner,  1951. First published 1931.

32. In 1961, Merton suggested that conflict and competition among lines
of social scientific development (and presumably in the physical and
biological sciences also) deserves study. Sociology of Science, p. 58.
It would appear that this problem has been preempted from further
attention until now.

33. Robert McGinnis,  "A scholastic model of social mobility," American
Sociological Review 33 (October 1968) 712-722. The axiom of cumulative
inertia holds that the longer an individual resides in a particular
location, the greater the probability of his remaining there. For its
application in science, Thomas Gieryn,  "Generational differences in
scientists'  research interests," Paper to be presented at the 1977
meeting of the American Sociological Association.
See Joel Yellin,  "A Model for Research Problem Allocation Among
Members of a Scientific Community,"  Journal of Mathematical Sociology
2 (1972): l-36 for a model emphasizing relations between population
growth in scientific communities, problem distribution and
specialization.

34. See Robert Jervis, Perception and Misperception in International
Politics.  Princeton: Princeton University Press, 1976. p. 187 ff. for
an insightful account of rigidity of perceptual sets in political
decision-making. The same observation can be problematic and
unproblematic for different investigators at the same time, see Bernard
Barber and Renee C Fox, "The Case of the floppy-eared rabbits: An

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instance of serendipity gained and serendipity lost," American Journal
of Sociology 64 (1958) 128-136.  It is surprising that so little
systematic work on error in science exists. See Jean Rostand, Error and
Deception in Science. Trnsd. A.J. Pomerans. New York: Basic Books, 1960.

35. Bacterial variation (the notion that bacteria were polymorphic) was
assumed to be an artifact of contamination after Koch developed a
usable procedure for pure cultures.  But genetic variation is not the
same as uncontrollable variation in experimental results. The latter is
generally defined as "noise" rather than phenomena of interest and
undermines the validity of observations, as Philip Teitlebaum reminded
us. Noise also makes certain problems aversive but for reasons
different from those noted here.

36. Labelling theory and studies of the impact of labelling on deviant
behavior are now active areas of investigation in sociology. See Edwin
Lemert,  Human Deviance Social Problems and Social Change. Englewood
Cliffs:  Prentice-Hall,  1972. Along different lines, Dorwin Cartwright,
in reviewing research on the "risky shift" in social psychology,
observes that the inept label persists in the face of accumulating
evidence that groups choose more rather than less conservative options
and that it has substantially delayed reorientation to the problem.
"Determinants of scientific progress:  The case of research on the Risky
Shift," American Psychologist.  28 (March 1[73) 222231. For a contrary
view on the impact of labelling this phenomenon,  see Franz Samuelson,
"Paradigms, Labels, and Historical Analysis," American Psychologist 29
(December 1973) 1141-1143.

37. Merton,  Sociology of Science, Ch. 13.

38. This was probably not so for Koch whose zeal to have the pure
culture method accepted universally may have led him to greater
dogmatism about the absence of bacterial variation than the evidence
required.

39. Martinus Beijerinck 1901, Mutation bei Bakterien. Versl. Akad.
Wetensch., Amsterdam, 9:310.

40. Beijerinck, Robert Olby writes, brought Mendel's work to de Vries'
attention and thus forced de Vries to acknowledge that he had been
anticipated by thirty-five years. Origins of Mendelism. New York:
Schocken Books, 1966. Pp. 127-128.

41. Joseph Needham,  "Limiting factors in the advancement of science as
observed in the history of embryology", Yale Journal of Biology and
Medicine 9 (1935-36) 1-18.

42. Derek J. de S. Price,  "Is technology historically independent of
science? A study in statistical historiography,  "Technology and Culture
7 (Fall 1965) 553-568.

43. Drawn from S.M. Lipset and EC. Ladd, "Jewish Academics in the
United States:  Their achievements,  culture and politics," American
Jewish Yearbook 1971, pp. 89-128, at p. 93.

44. Harriet Zuckerman, Scientific Elite. New York: Free Press, 1977.
Ch. 3. This finding no doubt reflects the fact that Jews are most often

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found in mobile fields such as molecular biology and theoretical
physics, precisely those which most often receive Nobel prizes.

45. Who's Who in America tends to underrepresent the business elite and
to overrepresent academic and clergymen. It is not clear whether these
biases would lead New Yorkers to appear more frequently in its pages or
less. Given municipal crime rates, New Yorkers are also apt to be
overrepresented among criminals as well. The sociology of New York and
of other great cities is still to be investigated.

46. Ira Risenwaike, Population History of New York City. Syracuse:
Syracuse University Press, 1972. P. 188 and U.A. Bureau of the Census,
Historical Statistics of the United States. Series A6-8. P. 8, Part I,
No.  93-98.

47. This finding is not consistent with data on the educational origins
of American scientists which show that New York state colleges produce
no more than their share of doctorates in science. R.H. Knapp and H.B.
Goodrich, Origins of American Scientists. Chicago: University of
Chicago Press, 1952. New York City colleges however may exhibit a
different pattern. Taking the City College and Columbia College as two
unrepresentative instances, we note that both have produced an excess
of doctorates in science relative to the number of their male
graduates. City College alumni get 2.3 times as many Ph.Ds. in science
as its alumni pool would predict and Columbia College alumni, 1.4 times
that number. Calculated from L. Harmon and H. Soldz, Doctorate
Production in United States Universities: 1920-1962. Washington, D.C.:
National Academy of Sciences-National Research Council, 1963. #1142,
Appendix 5 and Knapp and Goodrich, 1952, Appendix 4.

48. In this, the Lederbergs were only slightly atypical of families
producing American Nobel laureates in science. Laureates come from
families headed by professionals far more often than the run of
scientists but this does not mean that they were affluent. The fathers
of Nobelists who were professionals were usually professors, teachers
and physicians -- comparatively high in prestige and education but not
necessarily well-to-do. Zuckerman, Scientific Elite, Chapter 3.

48. Alexander W. Astin, "Undergraduate achievement and institutional
'excellence'," Science 161 (16 August 1968) 661-668 and "Undergraduate
institutions and the production of scientists," Science 141 (1963)
334-338. A recent study of collegiate origins of science doctorates
shows that institutions active in research in certain fields do not
conspicuously "overproduce" baccalaureates who go on in those fileds.
But it is clear that the colleges which graduate an excess of science
doctorates seem to specialize; their alumni are clumped in certain
sciences.  Studies of "school effects" are still insufficiently detailed
to account for the observed differences. Bruce Cathey,
"Science Recruitment Patterns in Baccalaureate Institutions: A Study of
Differential Ph.D. productivity by Field," Unpublished Master's Essay.
Department of Sociology, Columbia University. January 1977.

50. Francis Ryan and Joshua Lederberg, "Reverse-mutation and adaptation
in leucineless Neurospora," Proceedings of the NAtional Academy of
Sciences, U.S.A. 32 (June 1946) 163-174.

51. Tatum had weathered his own struggle for recognition at Stanford,

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having been labelled a chemist dubiously appropriate for a Biology
Department. He left in 1945 during a period of stagnation in the
department and the university.  This brief sojourn at Yale was of course
another item of good fortune for Lederberg. In 1948 Tatum returned as a
full professor. Cf 11). On problems encountered in redefining
departmental intellectual commitments and establishing new
interdisciplinary departments, see Peter M. Blau, The Organization of
Academic Work. New York: John Wiley, 1473. Pp. 189-216.

52. Recent work on social standing and risk-assumption in agriculture
is consistent with this general position. J.W. Gartrell, E.A. Wilkening
and H.A. Presser,  "Curvilinear and linear models relating status and
innovative behavior: A reassessment, I1 Rural Sociology 38 (1973)
391-411; D.E. Morrison,  "Review of Frank Cancien,  'Change and
Uncertainty in a Peasant Economy"', Contemporary Sociology 2 (1973)
262-265. A number of studies now find that social status and
willingness to assume risk are  linearly related.

53. On the accumulation of advantage in science, see Merton, Sociology
of Science, 439-459, Jonathan R. Cole and Stephen Cole, Social
Stratification in Science. Chicago: University of Chicago Press, 1973
and Zuckerman,  Scientific Elite, Ch. 3.

54. Merton, Sociology of Science, Chs. 14-16.

55. Merton, Sociology of Science, Ch. 13, first published 1942 and
Bernard Barber,  Science and the Social Order. New York: Free Press,
1952.

56. Warren 0. Hagstrom, "Competition in science," American Sociological
Review 39 (February 1974) 1-18, at p. 10.

57. James D. Watson, The Double Helix. New York: Atheneum, 1968.

58. Jerry Gaston, Originality and Competition in Science. Chicago:
University of Chicago Press, 1973; Hagstrom,  "Competition in science";
and Daniel Sullivan,  "Competition in bio-medical science: Extent,
structure and consequences, 'I Sociology of Education 48 (Spring 1975)
233-241. Experience with anticipation varies across the sciences and
with age and recent productivity of individual investigators.

59. Gaston, Originality and Competition, p. 118; Hagstrom,
VVCompetition", p. 9; Sullivan,  "Competition in bio-medical science", p.
238. 40. Merton,  Sociology of Science, p.  308n. First published 1957.
Sullivan, "Competition in bio-medical science," suggests that elite
scientists may also be very competitive but his data do not permit him
to draw solid conclusions on this. P. 237.

61. See J. Cairns, G. Stent, and J.D. Watson, eds. Phage and the
Origins of Molecular Biology. Cold Spring Harbor, N.Y.: Cold Spring
Harbor Laboratory of Quantitative Biology, 1966.

62. Merton, Sociology of Science, Chs. 12 and 13. The normative
structure in science and its role in scientists' behavior is a matter
of dispute and considerable skepticism among some sociologists of
science. Critics of the Mertonian formulation include: Barry Barnes,
"On the reception of scientific beliefs", in B. Barnes, ed., The

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Sociology of Science. Harmondsworth: Penguin, 1971. Pp. 269-291; S. B.
Barnes and R.G.A. Dolby, "The scientific ethos: A deviant viewpoint,"
European Journal of Sociology 11 (1970) 3-25; Michael Mulkay, "Norms
and Ideology in Science," Social Science Information 15 (1976) 637-656;
Ian Mitroff,  The Subjective Side of Science. New York: Elsevier, 1974.

63. A.E. Mirsky and A.W. Pollister,  Journal of General Physiology 30
(1946) 117.

64. R.D. Hotchkiss, "Gene,  transforming principle and DNA," in Cairns,
et al.  Phage, pp. 189-200, at p. 189.

65. Studies of the applications of science also treat discovery as a
process but from a somewhat different perspective. See J.H. Comroe and
R.D. Dripps,  "Scientific basis for the support of biomedical science,"
Science 192 (9 April 1976) 105-111.

66. H. Small and B. Griffith,  "The structure of scientific literature:
Identifying and graphing specialties," Science Studies 4 (1974) 17-40.

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Some afterthoughts on references
add to (33)

See Joel Yellin, "A Model for Research Problem Allocation Among
Members of a Scientific Community,"  Journal of Mathematical Sociology
2 (1972): l-36 for a model emphasizing relations between population
growth in scientific communities, problem distribution and
specialization.

Add to {65}

Project Hindsight:

C.W. Sherwin and R.S. Isenson, "First Interim Report on Project
Hindsight" Summary, 30 June 1966; revised 13 October 1966, No. AD
642-400, Clearinghouse for Federal Scientific and Technical Information,
Springfield, Virginia 22151.
770428     Yellin is redundant at lines 1778-83, 1985-9

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