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

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

After surveying a wide range of nineteenth and twentieth century medical and biological work, we chose a small number of disease-oriented research problems for close historical study, utilizing primarily a detailed tracing and analysis of primary sources. The examples we selected, drawn from bacteriology, nutrition, biochemistry, endocrinology, genetics, and immunology, are presented in the form of case studies. In addition to representing a range of biomedical inquiry that began with a clinical problem, these cases illuminate other aspects of the complex processes of research and discovery. They represent, too, a variety of ways of examining and presenting historical materials in the form of narrative essays. For, we would argue, just as there is no single way to "do" science, so too there is no single way to describe how it was done.

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

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

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

Our final two case studies, like the beriberi study, treat more specific disease problems, tracing how efforts to understand their causes and nature led, in often unforeseeable ways, to new understanding of fundamental biological phenomena. Thus, in Chapter 5 we examine the role that work on sickle cell anemia played in defining the genetic control of protein structure, while in Chapter 6 we follow a trail of researches that began in 1846 with the discovery of a strange urinary [END OF PAGE 1] product in a patient with multiple myeloma and ended in the 1960's with the first complete mapping of an antibody's molecular structure.

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

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

Blind Men and Elephants:
Labelling Biomedical Research

In the seventeenth century, historian Herbert Butterfield has observed, the "proper method" of scientific inquiry was "one of the grand preoccupations, not merely of the practicing scientist, but . . . amongst the general thinkers and philosophers" (Butterfield 1958, p. 97). Future historians, looking back upon science in the latter decades of the twentieth century, may judge that one of this period's "grand preoccupations" was the nature of and relationship between "basic" and 11 applied" research, or, in current biomedical parlance, between "basic" or "fundamental" and "categorical" or "mission -oriented" research.

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

Both in the past and today, arguments about the scientific and social roles of basic and applied research also have involved practical quests for patronage - for the support of researchers by public and private sponsors. In the recent history of biomedical research in the United States, much (but by no means all) of the concern about basic-applied distinctions has been linked with the emergence of the federal government as the major research patron in the years since World War 11. Social and economic policy decisions about how the patron should disperse his finite monies among many competing areas of research, in relation to various desired outcomes of that research, have generated an often heated dialogue about the nature of and "proper [END OF PAGE 2] balance" among various lines of biomedical investigation and have tended to foster a strict and competitive division between basic and applied research.

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

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

But if Johnson's call to "zero in on the targets" was not a new one, it was one that nonetheless had profound and receivers of federal funds for biomedical research. As Weinberg commented a few months after the event, "the world of biomedical research, at least that portion of it that regards itself as following the Newtonian tradition of research for it's own sake ,was thrown into a mild state of shock by the President's remarks (Weinberg 1967, p. 32). In retrospect, Johnson's remarks, and the responses to them from within and without the biomedical research community, was but one in a series of events and policy decisions at the end of the 1960's that signalled the start of a new fiscal and political era for biomedical research. After two decades of burgeoning growth, with the federal government as its major moral and financial supporter, the research enterprise faced new delivery oriented competitors such as Medicare for the nation's health dollars (Berliner and Kennedy 1970). A series of critical questions began to be asked, by many sectors of society: about how research priorities were being or should be decided, about the policy, or lack thereof, that had guided federally funded research efforts, and, as epitomized by President Johnson's statement, about what the "health payoffs" had been from the massive amounts of money, equipment, facilities, and manpower devoted to biomedical research in the years since World War 11.

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

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

Given the long history of concerns about defining the "nature" and "proper methods" of science, and the more recent social and political history of biomedical research, it is easy to understand why there has been of [END OF PAGE 3] late a "grand preoccupation" with the nature of the relationship between "basic and applied" research. And, as one reviews the literature that this preoccupation has generated, one appreciates Alvin Weinberg's cautionary words a decade ago: "that the question about the basic-applied relationship is once more asked in sharp and urgent terms, particularly with respect to biomedical research, by no means implies that new or particularly cogent insights have been attained" (Weinberg 1967, p. 33).

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

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

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

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

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

The struggle to carve up the biomedical research elephant according to such variables has produced in the past decade a profusion of studies, hearings, and reports and a sometimes bewildering array of terms. Thus, one can read discussions of basic research, fundamental research, intrinsic basic research, mission-oriented basic research, and non-mission-oriented basic research, and how these endeavors may differ from applied research, mission oriented research, targeted research, programmatic research, systematic research, and categorical research. And, in virtually every such discussion, there are caveats about how difficult it is, in practice, to apply these categories, about the complex feedbacks that occur between the various suggested types, and about t e continuum that is biomedical research (see, for example, Beecher, 1960; Bode 1965; Brooks 1965; Comroe and Dripps 1974, 1976; Frederickson 1977; Horsfall 1965; Kistiakowsky 1965; Shannon 1967; Stewart 1965, 1967). [END OF PAGE 4]

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

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

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

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

As Weiss in part suggests, there are a number of pragmatic reasons for making pronouncements about the identity of whatever part of the biomedical research elephant one is grasping. Each utterance may be a fair inference for the time, place, and reasons it is made, but in sum it is hard to make a whole elephant out of them. The discussion and categorization doubtless will continue, but it would be well to bear in mind their history. That history indicates that the efforts to categorize various types of research often have little relation to the actual doing of the research itself, nor that they will be of great utility in predicting where a given line of research will lead. As illustrated by the following two statements, this has long been realized by many investigators, and, more recently, by many who have sought to determine the shape of a national research policy.

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

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

Floppy-eared Rabbits and the Cult of Serendipity

In his 1945 volume of autobiographical essays, the distinguished physiologist Walter B. Cannon included a chapter entitled "Gains from Serendipity." In it he discussed a long recurrent theme in literature on the nature of science, a theme addressed particularly by scientists themselves: the role of chance or accident in research [END OF PAGE 5] and discovery. Serendipity, Cannon noted, was not a new term; it had been coined by Horace Walpoie nearly two hundred years earlier, But, until Cannon's essay, serendipity was an almost unknown word, and the great American physiologist surely had no prevision of how it would become used and misused, and elevated into a quasi-philosophical concept about a, if not the, dominant characteristic of basic research.

In 1754, Cannon wrote,

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

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

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

In more sophisticated statements, scientists may not be portrayed as people who blunder onto monumental discoveries. But, in discussions of the differences between basic and applied research, serendipity often is involked as the distinguishing characteristic of basic research, with little or no attempt to say what is meant by ascribing a scientific advance as due to chance. Rather, one usually reads simple declarative statements to the effect that serendipity is a major avenue to new knowledge or discovery in basic research, and hence the directions or outcomes of basic research, to a large extent, are uncertain, unpredictable, or uncontrollable (in contrast, that is, to applied research, which is characterized as being a programmatic or systematic progression toward clearly specified objectives). One of innumerable such characterizations of basic research is found in the Department of Health, Education, and Welfare's Forward Plan for Health, FY 1977-1981, in the section on "relative investments in fundamental and applied research." "Effective 'targeting' of resources to particular disease processes requires an adequate fundamental science base to be effective, but articulate exposition of the often serendipitous process of scientific advance is absolutely essential to greater public understanding of this process" (Forward Plan 1975, p. 70).

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

The same year that Cannon wrote of serendipity, for example, Robert K. Merton drew the attention of sociologists of science to "the serendipity pattern," describing it as involving the "unexpected, anomalous and strategic datum which exerts pressure upon the investigator for a new direction of inquiry which extends theory." By strategic, Merton emphasized, he was "referring rather to what the observer brings to the datum than to the datum itself" (Merton 1957, p. 104). For sociologists and their readers, Merton's point about the importance of what the observer or investigator brings to his chance encounter was given substance by Barber and Fox's now classic study of "the case of the floppy-eared rabbits." Theirs was an account of "serendipity gained and serendipity lost," exploring the reason why one clinical investigator pursued an unexpected observation: after rabbits received an intravenous injection of the proteolytic enzyme papain, their ears [END OF PAGE 6] collapsed. At about the same time, another researcher independently made the same observation, but his was an example of serendipity lost. Primarily because of his "research preconceptions and the occurrence of other serendipitous phenomena in the same experimental situation" he did not pursue the case of the floppy-eared rabbits, which eventually led to new knowledge about cartilaginous tissues (Barber and Fox 1957).

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

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

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

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

The same thesis about the investigator's critical role in ensuring gains from serendipity was stated briefly and elegantly by Louis Pasteur: "chance favors the prepared mind." And, as Cannon noted, "Even before Pasteur, Joseph Henry, the American physicist, enunciated the same truth when he said, "The seeds of great discoveries are constantly floating around us, but they only take root in minds well prepared to receive them" (Cannon 1945, pp. 75-76).

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

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

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

When W. B. Cannon borrowed the word serendipity from Horace Walpole, he used it merely to symbolize the fact that scientific investigators are likely to discover many interesting facts other than the ones they are looking for. Oddly enough, this simple concept has been given so much importance and dignity during the past few decades that it has become a dominant scientific philosophy. If one were to judge from much recent writing, even by some scientists, the justification for doing research on almost any subject is the statistical chance of achieving by accident, useful [END OF PAGE 7] and practical results. It would be out of place to discuss here the historical fallacies on Which this belief is based. I cannot refrain, however, from stating my view that the cult of serendipity is based on an erroneous interpretation of the history of science, and furthermore amounts to an abdication of intellectual and ethical responsibility. Serendipity is the equivalent of Stephen Vincent Benet's line, "We don't know where we're going, but we're on our way." (Dubos 1967, p. 128) [END OF PAGE 8]


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