Reprinted from Nature, Vol. 324, No. 6098, pp. 629-631, 18 December 1986
          0 Macmillan Journals Ltd., I986

Postmature scientific discovery?

Harriet Zuckerman and Joshua Lederberg

NEW scientific discoveries do not always
flow directly from those made just before.
Rather, several varieties of discontinuity
can be identified in the growth of science.
Premature discoveries are those that sci-
entists do not attend to in a timely way,
and are retrospectively described as hav-
ing been "ahead of their time". These
have been examined by Barber' and
Stent'. Here, we suggest that there are
also postmature discoveries, those which,
are judged retrospectively to have been
`delayed'. We analyse the arguments that
the discovery of bacterial sex was postma-
ture and take up the correlative questions
of how the problem was identified, and
why Lederberg and Taturn'," were likely
candidates for making it when they did.

This paper draws on documents, pub-
lished and private, and analyses by the
sociologist-observer and the scientist-
participant. Our dialectic procedure de-
parts from most oral histories'.h; first, the
procedure was iterative: as new discussion
raised further possibilities, we both sear-
ched for relevant documentation; and
second, we both identified the underlying
analytic questions and articulated tenta-
tive answers to them. We felt that per-
sonal reminiscence had to be validated by
contemporary documents and other testi-
mony as oral history and autobiography
are prone to "unconscious falsification"`.

Continuities and discontinuities
Scientific growth, usually broadly incre-
mental, can at important times be episodic
and discontinuous. Premature discover-
ies, one conspicuous form of temporal dis-
continuity in science, are either passively
neglected or actively resisted at the time
they are made. Mendel's discovery of par-
ticulate inheritance in 1865, lost to view
for thirty-five years, is the best-known his-
torical case. Discoveries can be premature
because they are conceptually miscon-
netted with `canonical knowledge", are
made by an obscure discoverer, published
in an obscure place, or are incompatible
with prevailing religious and political doc-
trine. Barriers between disciplines im-
posed by specialization of inquiry also
contribute to neglect or resistance'.r"`.
Although the character and sources of
premature discoveries have received some
analytical attention',", the pattern of post-
mature discoveries has not been identi-
fied, much less systematically studied.

For a discovery to qualify as post-
mature, for it to evoke surprise from the
pertinent scientific community that it was
not made earlier, it must have three attri-
butes. In retrospect, it must be judged to
have been technically achievable at an

earlier time with methods then available.
It must be judged to have been under-
standable, capable of being expressed in
terms comprehensible to working scientists at
the time, and its implications must have been
capable of having been appreciated.

Both prematurity and postmaturity can
be recognized only by retrospection. They
differ in that prematurity is a matter of
actual historical observation while post-
maturity is a matter of retrospective con-
jecture. Such formulations would seem to
smack of `Whig History', the inclination,
according to Butterfield, "to produce a
story which is the ratification if not the
glorification of the present"`*. But, they
are designed to serve quite the contrary
purpose. The ideas of premature and post-
mature discovery provide convenient
handles for analysing discontinuities in the
growth of scientific knowledge, and sup-
port a nonlinear and complex model of
advancement in scientific understanding.

Postmature discoveries are not all of a
piece. One class results from pre-emption
of scientists' research attention. For exam-
ple, Linus Pauling observed that there was
"no reason why" he, himself, could not
have discovered the alpha helix eleven
years earlier than he actually did "after a
few hours of work". In fact, he was preoc-
cupied in the interval by other seemingly
more important and feasible inquiries" I'.
Another class of postmature discoveries
answer questions not previously recog-
nized by scientists to be problematic. Cer-
tain assumptions, beliefs and images"
which are also indispensable for the orga-
nization of scientific thought can, in speci-
fic cases, impede perception of lines of
inquiry. For example Weinberg notes that
physicists neglected to pursue quantum
field theory further in the 1930s because
prevailing images, conceptual schemes
and attitudes toward theory and empirical
evidence stood in the way". In our case
study, both cognitive and social processes
obstructed the thinking of scientists about
recombination in bacteria.

Sources of neglect

Why was recombination in bacteria not
perceived as problematic before 1946?
HOW had asexuality in bacteria come to be
an unquestioned `truth' and how was that
view perpetuated?

Before 1870, many believed that the
different shapes bacteria assumed were
varieties of the same organism, which
changed under varying conditions. In-
deed, the doctrine of polymorphism or
bacterial plasticity became the basis for
extravagant claims about variability
through most of the nineteenth century.

By 1872, Ferdinand Cohn concluded that
the various shapes bacteria took were not
different forms of the same organism; they
were monomorphic and did not change
during their short lifetimes". Yet reports
of variation continued until 1881 when
Robert Koch introduced a simple and
effective means for growing pure cultures.
Koch's pure-culture method, which be-
came a symbol of modern bacteriology
with its phobia of contamination, together
with Cohn's doctrine of monomorphism
rapidly changed bacteriologists' views ab-
out variation. The two were consolidated
into what was called the Cohn-Koch
Dogma, which discouraged for years the
study of the problems of morphology.
inheritance and variation in bacteria".

Cohn was convinced that bacteria were
primitive plants which could "only repro-
duce by asexual means" and in 1875 char-
acterized all bacteria as Schizomycetes or
`fission fungi'. With every use of that
label, bacteriologists were reminded that
these organisms reproduced only by fis-
sion and that they were simple primitive
plants, a tradition that had begun with
Leeuwenhoek's first observation of bac-
teria in 1675. Labels, categories, nomen-
clature and taxonomies usually help to
organize scientific thought but can also
delay the reexamination of fallacious tra-
ditions,  thus becoming self-fulfilling
prophecies'". In the end, the emergence of
medical microbiology as a science de-
pended on the doctrinal base laid down by
Cohn and the pure culture methods of
Koch. Nonetheless, monomorphic doctri-
ne, when strictly construed, threw out the
baby of bacterial variation with the dirty
bath water of contamination. It was wide-
ly assumed that observations of bacterial
variation had to result from contamina-
tion. Bacteriologists took experiments in-
volving variation to be error-prone and
disreputable'". Such experiments were to
be avoided as having great procedural dif-
ficulty and little intellectual merit. With
the strong incentives in science for avoid-
ing problems notorious for leading to
irreproducible results, very few scientists
would elect to undertake them.

Bacteria occupied an ambiguous place
in the hierarchy of living organisms. To
many, these organisms appeared so primi-
tive that they could not yet have evolved
`differentiated genes'. This image also
reinforced the use of bacteria as exemp-
lars of pre-genie levels of organization for
physico-chemical analysis. Once such
complex imagery becomes established,
special provocation is needed to splinter
away one or more of its elements.

Disciplinary emphases and the division


2

of labour among the sciences also diverted
attention from the problem of bacterial
sexuality. Bacteriologists were principally
concerned with problems in medical
pathology rather than issues like the bio-
logy of bacterial reproduction. Geneticists
were no more interested in bacterial rep-
roduction than bacteriologists. They were
occupied with larger organisms in which
the products of crossing were readily
observed. Thus, disciplinary division of
labour and the careful choice of organisms
for inquiry, both generally conducive to
the development of scientific knowledge,
contributed in this instance to neglect of
bacterial recombination. It has been
argued, however, that `disciplinary dog-
matism' and `disciplinary monopoly' have
only rarely impeded the development and
diffusion of scientific innovation".

Members of the Delft School of Micro-
biology, in the early part of this century,
did bridge the gap between bacteriology
and genetics. Clearly separating them-
selves from the medical bacteriologists
who maligned bacteria, they believed that
progress in fundamental microbiology de-
pended on people who `loved' microbes".
Martinus Beijerinck, the main figure in
the group. seems now to have been the
most likely candidate for investigating
bacterial sex. He rejected prevailing dog-
ma on bacterial invariability, promptly
cited de Vries' finding on plant mutations
and offered some of the first coherent
challenges to strict monomorphism". He
also developed  `enrichment culture'
methods, forerunners of the selective
techniques used later in discovering bac-
terial recombination. Moreover, he was
better informed than most microbiologists
about work on plant hybridization which
would have been useful in planning any
investigation of sex in bacteria. Beijerinck
and the Delft School were likely candi-
dates for investigating bacterial sex, but
they did not. In fact, Beijerinck strongly
supported the Cohnian dogma of Schi-
zomycetes. Thus the problem of sexual
recombination still fell between disciplin-
ary schools".

Significance of bacterial sex
By the 193Os, developments were under
way that led biologists to reexamine how
bacteria related to other forms of life and
whether bacteria really had genes. Impor-
tant among these developments was the
unification in biological thought of Men-
delian genetics, quantitative population
theory and darwinian evolution, particu-
larly the notion of species being Mende-
lian breeding populations or isolated gene
pools. The idea that sexuality was, itself,
an evolved genetic system proved particu-
larly provocative, with illustrations drawn
from simple and complex plant life. Dob-
zhansky's monograph, "Genetics and the
Origin of Species"`5, was widely read as the
definitive reinterpretation of darwinian

theory of evolution and focused interest
on the details of breeding systems as the
key to understanding evolutionary de-
velopment. This, in turn, sharpened in-
terest in understanding the evolution of
organisms, like bacteria, believed to be
devoid of sexual mechanisms.

The biochemical analysis of microbial
nutrition,  especially by Knight and
Lwoff'", was another major impetus to
reexamining the relationship of bacteria
to other forms of life. In particular, the
discoveries that the biochemistry of mic-
robes paralleled in many details that of
higher organisms inspired Beadle and
Tatum's work on Neurospora in 1941Z6.
They showed Neurospora's usefulness as a
research material for studying the genetic
control of an organism's development
through the encoding of specific enzymes,
known as the  `one-gene-one-enzyme'
hypothesis. This marriage of biochemistry
and genetics had particular significance for
the Lederberg-Tatum work*`.`*.

There was also renewed speculative in-
terest in a biochemical theory of the origin
of life. "The Origin of Life on Earth"" by
the Russian biochemist, Oparin, became
available in English in 1944, as did "What
is Life?"" by the physicist Schriidinger.
Both focused attention on questions that
demanded the integration of the biology
of viruses and microbes with the more
traditional biology of plants and animals.

The connections between these inde-
pendent developments were not always
apparent at the time. But one event did
call attention to their common message;
the discovery by Avery, MacLeod and
McCarty in 1944 which identified DNA as
the transforming principle that changed
rough non-pathogenic pneumococci into
smooth virulent ones."

The scientific significance of that dis-
covery has been examined in detail"-lR.
For our purposes, it highlighted two im-
portant questions: what was the structure
of bacterial genes and how were they
transferred? Thus the work by Avery et al.
made the question of bacterial sex newly
consequential. Dubos" makes it clear that
had sexual reproduction been observed. it
would have been understood and appreci-
ated. But bacteria were so widely assumed
not to reproduce sexually that noone con-
sidered this problem to be important.
Dogma prevailed over focused curiosity.

Structural contexts

In retrospect, Lederberg's position in the
communication network and his not yet
having a career in science seem conse-
quential for his identifying the problem of
bacterial sex, for his developing a method
for its investigation and for his being in a
position to do the research. Tatum was led
to the problem independently for some-
what different reasons". Lederberg was
unenthusiastic about classical genetics
when he arrived at Columbia College in

1941. His interest in "understand[ing] the
chemical nature of life" led him to spend
much of the next four years studying
chemistry, cytology and physiological
embryology. But he was not ignorant of
classical genetics and the Columbia
biologists were well connected with the
New York network of scientific communi-
cation about genetics. Dobzhansky was a
central figure. Arthur Pollister was in clo-
se touch with researchers at the Rockefel-
ler Institute. Alfred Mirsky worked at
both institutions. Lederberg not only
learned quickly about the neo-darwinian
developments described earlier but he
also heard about the work of Avery et al.
from Mirsky and promptly read their pap-
er. If the Avery et al. work sharpened
Lederberg's interest in bacterial reproduc-
tion, Dubos' review of the inconclusive-
ness of evidence on sexual reproduction
sharpened his scepticism; the cognitive
and structural elements were coalescing.

In Lederberg's second year at Columbia
he met Francis Ryan, an assistant profes-
sor, who had just completed a post-
doctoral fellowship at Stanford with Bea-
dle and Tatum. It was Ryan who first told
him about the work on biochemical gene-
tics and who persuaded him that chemistry
and genetics were not as far apart as he
had thought". It was also Ryan who gener-
ously provided Lederberg with laboratory
facilities, catalysed his association with
Tatum, and, most importantly, encour-
aged, educated and socialized him as a
scientist. Columbia provided Lederberg
with a multifaceted and advantageous
structural context for his scientific de-
velopment and for the initiation of a high-
risk, high-stakes research programme.

Lederberg's plan for research was well
worked out by July 1945, when he was a
second-year student at Columbia Medical
School but continued to work in Ryan's
laboratory. The research might have been
pursued at Columbia, but Ryan and
Lederberg both recognized that an asso-
ciation with Tatum would be valuable. In
particular, his experience in microbial
biochemistry could help broaden Leder-
berg's education beyond the opportunities
available on Morningside Heights. Furth-
ermore, Tatum, then in the process of
moving to Yale, was rapidly becoming
recognized as a scientific leader. He could
provide Lederberg with better access not
only to information, research materials
and fellowship support, but also to the
invisible college of the emerging scientific
discipline of biochemical genetics. The
impact of such informal ties between in-
vestigators on the directions and pace of
scientific research has yet to be properly
investigated.

Lederberg's status as a medical student
was less an obstacle to his investigating
bacterial sex than might be supposed.
Though much of his time was spent on
course work, he was not subject to the


constraints that apply in the early years of
study for the PhD. He did not, like ordin-
ary graduate students, have to choose a
research problem that would be suitable
for a thesis and publication, Being
marginal" to the biological research enter-
prise, he could afford to take on a high-
risk problem. The search for bacterial sex
was definitely high-risk; it was not one
likely to produce useful and publishable
findings. After all, not observing bacteria1
recombination would scarcely demons-
trate that it did not exist. The risk of a
negative finding using E. coli is now
known precisely; bacteria1 recombination
being observed in only five per cent of all
strains with the techniques used in 1946.

For a different set of reasons, Tatum
could also afford research on a high-risk
problem at the time. He had a variety of
projects in process in his laboratory and
could manage to take a long-shot experi-
ment that required little time and little
money. For both men, bacterial recom-
bination was a good gamble; failure would
have low marginal costs for each but
promised large if prospectively improb-
able returns. High-risk investigations are
not equally feasible for all scientists. They
fall to the comparatively well-established
or to those who are marginal as Lederberg
was in 1946. Those who solve high-risk
problems, having chosen them in the first
place, may more often come from the ranks
of the well established than from neophytes
thus contributing to he accumulation of
advantage". Risk-taking in science is a mat-
ter not only of psychological daring but
also of position in the social structure'4.42.

After a brief correspondence, Tatum
invited Lederberg to work at Yale. He
arrived in March 1946; genetic recombina-
tion in E.  cofi was experimentally
observed early in May. The results were so
arresting that Tatum arranged for Leder-
berg to present them at the Cold Spring
Harbor Symposium to be held in July. The
publications which fo110wed'.4,43 did not
merely describe the results of the initial
laboratory investigation. They are the
product of critical discussion of those re-
sults at that meeting and of follow-up ex-
periments done immediately afterwards".
The dynamics of organized scepticism in
sciencea can be observed in the records of
that meeting and later in responses to the
papers announcing the discovery. Even as
first published, discoveries are not simply
reports of events intially observed in the
laboratory4'.* but often are also the out-
comes of exchange between contributors
and their critics. Treating scientific contri-
butions as the results of inquiry, criticism
and subsequent work makes problematic
the custom of designating this or that sci-
entist as the exclusive contributor and
focusses attention on the operation of
organized scepticism and its effect on
shaping the meaning and assessment of
those contributions.

Conclusions

Was the investigation of sexual recom-
bination in bacteria postmature, that is,
conducted significantly later than it could
have been? The problem was obscured for
decades by the Cohn-Koch dogma of
monomorphism and the conviction that
bacteria1 variation resulted only from con-
tamination. This was so even for Bei-
jerinck and members of the Delft School
who did not subscribe to strict monomor-
phism, knew how to mark microbial
strains by their fermentative and nutritio-
nal characteristics (the basis of Leder-
berg's design), knew about Mendelian
segregation in plants, and might have
appreciated the significance of sexual re-
combination in bacteria were it observed.
But, they were committed to the view that
bacteria reproduced only by fission and
did not consider the phenomenon prob-
lematic. In principle, the investigation was
technically feasible by 1908, as demons-
trated by Browning's" use of drug resist-
ance as a selective marker, an early anti-
cipation of the Lederberg-Tatum work.
But Browning dealt with a different
organism, reported a negative result, and
used terminology not readily transferable
to the case of bacterial recombination. In
the 1930s bacterial sex was still viewed as
unlikely, even as a disreputable idea. Yet
had it been demonstrated experimentally,
it would have been understood and appre-
ciated by geneticists and possibly even by
bacteriologists.

This case study suggests that problem-
identification and selection in science
have features deserving further analysis.
First, the solutions to two classes of prob-
lems are apt to be postmature: those
which do not survive competition for sci-
entists' attention when they first appear
because they seem insignificant, unfeasi-
ble or both and those which are obscured
by prevailing cognitive commitments or
have no socially and cognitively defined
disciplinary home. Second, in calculating
the probable returns on selecting prob-
lems for investigation, scientists assess the
likelihood of error and this contributes to
the continuing neglect of certain problems
that have a history of being error-prone.
Third, the feasibility of addressing high-
risk problems in science and so of making
major advances in this way is not equal for
all investigators; they are left largely to the
well-established who can afford them and
to others who have a smaller stake, for
structural reasons, in their immediate re-
cord of publication. What scientists define
as problematic and worthy of investiga-
tion are the products of interactions be-
tween cognitive and social processes.

Research supported by NSF Foundation
(SES 84-l I IQ), the Russell Sage Foundation
and the Center for Advanced Study in the
Behavioural Sciences.

Harriet Zuckerman ts at the Department of'
Sociology. Columbia University, New York,
New York 10027, USA and Joshua Lederherg 1s
at The Rockefeller University, I230 York Ave-
nue, New York, New York 10021. USA.

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