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Prematurity in Scientific Discovery: On Resistance and Neglect / Edition 1

Prematurity in Scientific Discovery: On Resistance and Neglect / Edition 1

by Ernest B. HookErnest B. Hook


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For centuries, observers have noted the many obstacles to intellectual change in science. In a much-discussed paper published in Scientific American in 1972, molecular biologist Gunther Stent proposed an explicit criterion for one kind of obstacle to scientific discovery. He denoted a claim or hypothesis as "premature" if its implications cannot be connected to canonical knowledge by a simple series of logical steps. Further, Stent suggested that it was appropriate for the scientific community to ignore such hypotheses so that it would not be overwhelmed by vast numbers of false leads. In this volume, eminent scientists, physicians, historians, social scientists, and philosophers respond to Stent's thesis.

Product Details

ISBN-13: 9780520231061
Publisher: University of California Press
Publication date: 10/02/2002
Edition description: First Edition
Pages: 398
Product dimensions: 6.00(w) x 9.00(h) x 1.20(d)
Lexile: 1340L (what's this?)

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Prematurity in Scientific Discovery

On Resistance and Neglect

The University of California Press

Copyright © 2002 Regents of the University of California
All right reserved.

ISBN: 0-520-23106-6

Chapter One

Prematurity in Scientific Discovery Gunther S. Stent

One of the depressing by-products of the fantastically rapid progress that was made in molecular genetics in the past twenty-five years is that now merely middle-aged participants in its early development are obliged to look back upon their early work from a depth of historical perspective that, in the case of biological specialties that came into flower in earlier times, had opened up only after all the witnesses of the first blossoming were long dead. I have been trying to make virtue out of necessity and actually exploit this singular position for fathoming the evolution of a scientific field. Thus, in looking back on the history of molecular genetics from the viewpoint of my own experiences, I have found that one of its most famous incidents, Oswald T. Avery's identification of DNA as the active principle in bacterial transformation and, hence, as genetic material, illuminates a general problem of cultural history. The case of Avery brings, I think, insights into the question of whether it is meaningful, or merely tautological, to allege that a discovery is "ahead of its time," or premature.


In 1968, I published a briefretrospective essay on molecular biology with particular emphasis on its origins. In this historical account, I mentioned neither Avery's name nor DNA-mediated bacterial transformation. My essay brought forth a letter to the editor by Carl Lamanna, who complained that "it is a sad and surprising omission that Stent makes no mention of the definitive proof of DNA as the basic hereditary substance by O. T. Avery, C. M. MacLeod and I. L. McCarty. The growth of [molecular genetics] rests upon this experimental proof.... I am old enough to remember the excitement and enthusiasm induced by the publication of the paper by Avery, MacLeod and McCarty. Avery, an effective bacteriologist, was a quiet, self-effacing, non-disputatious gentleman. These characteristics of personality should not prevent the general scientific public represented by the audience of Science to let his name go unrecognized."

I was taken aback by Lamanna's letter and replied that I agreed that I should have really mentioned in my essay Avery's proof in 1944 that DNA is the hereditary substance. But, I went on to say, in my opinion it is not true that the growth of molecular genetics rests upon Avery's proof. For many years that proof had actually made a surprisingly small impact on geneticists, both molecular and classical, and it was only the Hershey-Chase experiment of 1952 which caused those people to focus on DNA. The reason for this delay was neither that Avery's work was unknown to or mistrusted by geneticists nor that the Hershey-Chase experiment was technically superior. Instead, Avery's discovery, so I declared, had been merely "premature." And in the last two sentences of my reply to Lamanna, I sketched out the argument about prematurity that I shall try to develop here in somewhat greater detail.

My prima facie reason for considering Avery's discovery premature is that it was not appreciated in its day. But is it, in fact, true that Avery's discovery was not appreciated? Lamanna, for example, mentions his own excitement and enthusiasm induced by the publication of Avery's paper, and several participants in the 1946 Cold Spring Harbor Symposium on Heredity and Variation in Microorganisms have told me that Avery's discovery formed the subject of intense discussion at that symposium. So how can I say that it was not appreciated? By lack of appreciation I do not mean that Avery's discovery went unnoticed, or even that it was not considered important. What I do mean is that no one seemed to be able to do much with it, or build upon it, except for the students of the transformation phenomenon. That is to say, Avery's discovery had virtually no effect on general genetic discourse.

By way of support of this allegation, I invite examination of the 1946 Cold Spring Harbor Symposium volume. It contains a paper by McCarty, Harriet Taylor, and Avery, whose main concern is not the meaning of the discovery for genetics but the elucidation of the role of serum in the DNA-mediated transformation phenomenon. Although many of the other papers of the volume are followed by discussants' remarks, no discussant of the McCarty, Taylor, and Avery paper is on record. Only five of the other 26 symposium papers refer to Avery's discovery.

Three phage workers, T. F Anderson, A. D. Hershey, and S. E. Luria, venture the opinion that the phenomenon is probably of wide biological importance. L. Dienes concludes that since DNA is "a substance without apparent organization," Avery's discovery means that "bacteria possess a mechanism for the exchange of hereditary characteristics, [that is] different from the usual sexual processes," and S. Spiegelman is under the impression that Avery discovered "the induction of a particular enzyme with a nucleoprotein [sic] component." Neither Max Delbrück nor J. Lederberg and E. L. Tatum mention Avery at all in their now famous 1946 symposium papers.

An even more convincing demonstration of the lack of appreciation of Avery's discovery is provided by the 1950 Golden Jubilee of Genetics symposium "Genetics in the 20th Century." Here some of the most eminent geneticists of that time presented essays that surveyed the progress of the first 50 years of genetics and assessed its present status. Only one of the 26 essayists saw fit to make more than a passing reference to Avery's discovery, then six years in the past, namely A. E. Mirsky, who still expressed some doubts that the active transforming principle is really pure DNA. H. J. Muller's 1950 symposium essay on the nature of the gene contains no mention of Avery or DNA.

So, why was Avery's discovery not appreciated in its day? Because it was "premature." But is this really an explanation or is it merely an empty tautology? In other words, is there a way of providing a criterion of the prematurity of a discovery other than its failure to make an impact? Yes, there is such a criterion: A discovery is premature if its implications cannot be connected by a series of simple logical steps to contemporary canonical [or generally accepted] knowledge. This criterion is not to be confused with that of an unexpected discovery, which can be connected with the canonical ideas of its day but might overthrow one or more of them. For instance, the finding of a "reverse transcriptase" would fall into the category of unexpected discoveries-provided, of course, that the function attributed to that enzyme of catalyzing the assembly of a DNA replica from an RNA template can eventually be shown to occur in vivo. Although prior to that finding, it had been generally assumed by molecular geneticists that there is no reverse flow of "information" from RNA to DNA, there is no difficulty at all in understanding such a process from the viewpoint of the previous current ideas of polynucleotide synthesis.

Why could Avery's discovery not be connected with canonical knowledge? By 1944, DNA had long been suspected of exerting some function in hereditary processes, particularly after R. Feulgen [with H. Rossenbeck] had shown in 1924 that DNA is a major component of the chromosomes. But the then current view of the molecular nature of DNA made it well nigh inconceivable that DNA could be the carrier of hereditary information. First of all, until well into the 1930s DNA was generally thought to be merely a tetranucleotide composed of one residue each of adenylic, guanylic, thymidylic, and cytidylic acid. Secondly, even when it was finally realized by the early 1940s that the molecular weight of DNA is actually much higher than that demanded by the tetranucleotide theory, it was still widely believed that the tetranucleotide is the basic repeating unit of the large DNA polymer in which the four purine and pyrimidine bases recur in regular sequence. DNA was therefore viewed as a monotonously uniform macromolecule which, like other monotonous polymers such as starch or cellulose, is always the same no matter what its biological source. The ubiquitous presence of DNA in the chromosomes was, therefore, generally explained in purely physiological or structural terms. Instead, it was usually to the chromosomal protein that the informational role of the genes had been assigned since the great differences in the specificity of structure that exist between heterologous proteins in the same organism, or between homologous proteins in different organisms, had been appreciated since the beginning of this century. The conceptual difficulty of assigning the genetic role to DNA had by no means escaped Avery, for in the conclusion of his paper he states that "if the results of the present study of the transforming principle are confirmed[,] then nucleic acids must be regarded as possessing biological specificity the chemical basis of which is as yet undetermined."

However, by 1950, the tetranucleotide theory had been overthrown, thanks largely to the work of Erwin Chargaff who showed that, contrary to the demands of that theory, the four nucleotide bases are not necessarily present in DNA in equal proportions. Chargaff found, furthermore, that the exact base composition of DNA differs according to its biological source, suggesting that DNA may not be a monotonous polymer after all. So when, two years later, Hershey and Chase showed that upon infection of the host bacterium at least 80% of the phage DNA enters the cell whereas at least 80% of the phage protein remains outside, it was now possible to connect their conclusion that DNA is the genetic material with canonical knowledge. For Avery's "as yet undetermined" chemical basis of the biological specificity of nucleic acids could now be envisaged as the precise sequence of the four nucleotide bases along the polynucleotide chain. The general impact of the Hershey-Chase experiment was immediate and dramatic. DNA was suddenly in and protein was out, as far as thinking about the nature of the gene was concerned. Within a few months, there arose the first speculations about the genetic code, and Watson and Crick were inspired to set out to discover the structure of DNA.

Naturally, the case of Avery is only one of many premature discoveries in the history of science. I have presented it here for consideration mainly because of my own failure to appreciate it when I joined Delbrück's phage group and took the Cold Spring Harbor phage course in 1948. Since then, I have often wondered what my later fate would have been if only I had been intelligent enough to appreciate Avery's discovery and infer from it four years before the Hershey-Chase experiment that DNA must also be the genetic material of the phage.

Probably the most famous case of prematurity in the history of biology is that of Gregor Mendel, whose discovery of the particulate nature of heredity in 1865 had to await 35 years before it was "rediscovered" at the turn of the century. Mendel's discovery made no immediate impact, so it can be argued, because the concept of discrete hereditary units could not be connected with the (mid 19th century) canonical knowledge of anatomy and physiology. Furthermore, the statistical methodology by means of which Mendel interpreted his data was wholly foreign to the way of thinking of his contemporary biologists. By the end of the 19th century, however, chromosomes, mitosis, and meiosis had been discovered, and Mendel's results could now be accounted for in terms of microscopically visible structures and processes. Furthermore, by then the application of statistics to biology had become commonplace. In some respects, however, Avery's case is a more dramatic example of prematurity than Mendel's. Whereas Mendel's discovery seems to have been hardly mentioned by anyone until its rediscovery, Avery's discovery was widely discussed, and yet could not be appreciated for eight years.

A striking example of delayed appreciation of a discovery in the physical sciences, as well as an explanation of that delay in terms of the concept to which I refer here as prematurity, has been provided by Michael Polanyi. In the years 1914-1916, Polanyi published a theory of the adsorption of gases on solids which assumed that the force attracting a gas molecule to a solid surface depends only on the position of that molecule, but not on the presence of other molecules, in the force field. Despite the fact that Polanyi was able to provide strong experimental evidence in favor of his theory, it was generally rejected. Not only was the theory rejected, but it was considered so ridiculous by the leading authorities of the time that Polanyi believes continued defense of his theory would have ended his professional career had he not managed to publish work on other more palatable ideas. The reason for the general rejection of Polanyi's adsorption theory was that, at the very time he put it forward, the role of electrical forces in the architecture of matter had just been discovered. And hence, there seemed to be no doubt that gaseous adsorption must also involve electrical attraction between gas molecules and solid surfaces. That point of view, however, was irreconcilable with Polanyi's basic assumption of the mutual independence of individual gas molecules in the adsorption process. Instead of Polanyi's theory, the theory of I. Langmuir, which did envisage a mutual interaction of the gas molecules of the kind expected from electrical forces, found general acceptance. It was only in the 1930s after F. London developed his new theory of cohesive molecular forces based on quantum mechanical resonance rather than electrostatic attraction, that it became conceivable that gas molecules could behave in the way in which Polanyi's experiments indicated they are actually behaving. Meanwhile, Langmuir's theory had become so well-established, and Polanyi's had been consigned so authoritatively to the ash can of crackpot ideas, that Polanyi's theory was rediscovered only in the 1950s.

We may now consider whether the notion of prematurity is actually a useful historical concept. First of all, is prematurity the only possible explanation for the lack of contemporary appreciation of a discovery? No, evidently not. For instance, Lamanna suggested the "quiet, self-effacing, non-disputatious" personality of Avery as the cause for the failure of general recognition of his discovery. And Chargaff is another believer in the idea that personal modesty and reticence for self-advertisement accounts for lack of contemporary appreciation. For instance, Chargaff has attributed the 75-year hiatus between F.


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