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. 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