Scientists' Competitive Behavior Is Not Peculiar To Our Competitive Age

Scientists' Competitive Behavior Is Not Peculiar To Our Competitive Age Author: Robert K. Merton, pp.12 century, America's preeminent science historian/sociologist, Robert K. Merton, has played a valuably instructive role in analyzing the processes of science and in elucidating the research world's manners and mores. The recipient of many awards, the 84-year-old Merton-- University Professor Emeritus at Columbia University in New York and a member of the National Academy of Sciences for the past quarter-century--was most recently honored by the American Council of Learned Societies. In April, he was invited to deliver the Washington, D.C., organization's prestigious Haskins Lecture to cap the 75th-anniversary celebration of its founding. The author of numerous influential works--most notable, perhaps, his 1965 book On the Shoulders of Giants: A Shandean Postcript (3rd ed., University of Chicago Press, 1993)--Merton has achieved international acclaim for the pertinence and applicability of his subject matter, the scope and precision of his scholarship, the durability of his conclusions, and the colorful persuasiveness of his discourse, all of which are evident in the following essay. The essay uses as its departure point a reference to The Double Helix, James Watson's deeply personal 1968 account of his and Francis Crick's discovery of the DNA molecule's structure. As Merton points out, Watson's rhapsodic joy over having been, with Crick, the first to achieve this epochal breakthrough confirmed the notion that scientists are capable of being "all too human" in their hotly competitive pursuit of accomplishment and its accompanying fame. The propriety of researchers' blatant ego involvement in their investigations is a subject that Merton explores in this essay--with conclusions that are as incisive and relevant today as they were 26 years ago. The following is drawn from the Sigma Xi-Phi Beta Kappa speech Merton delivered before the American Association for the Advancement of Science in December 1968 and published in full under the title "Behavior Patterns of Scientists." The full text of the essay is included in a collection of his works titled The Sociology of Science: Theoretical and Empirical Investigations (University of Chicago Press, 1973). The excerpt is presented here with permission of the publisher. James Watson fluttered the dovecotes of academia, to say nothing of the wider reading public, by telling us of having joined with Francis Crick in an enthusiastic toast "to the Pauling failure.... Though the odds still appeared against us, Linus had not yet won his Nobel." It would seem that Watson had violated the mores that govern contest behavior in science and the public disclosure of that behavior. Yet, how mild and restrained is this episode by comparison with judgments on contemporaries set out in public by great scientists of the heroic past. Although historical facts to the contrary are abundantly available, there emerges a new mythology that treats competitive behavior of scientists as peculiar to our own competitive age. This introduces an instructive paradox. These, indeed, are changing times in the ethos of science. But Watson's brash memoir does not testify to a breakdown of once-prevailing norms that call for discreet and soft-spoken comment on scientific contemporaries. A memoir such as his would have been regarded as a benign model of disciplined restraint by the turbulent scientific community of the 17th century. That it should have created the stir it did testifies that, with the centuries-long institutionalization of science, the austere mores governing the public demeanor of scientists and the public evaluation of contemporaries have become more exacting rather than less. As a result, Watson's little book, so restrained in substance and so mild in tone by comparison with the caustic and sometimes venomous language of, say, Galileo or Newton, violates the sentiments of the many oriented to these more exacting mores. All of this brings us to the question touched off by the responses of many scientists and laymen to the Watson memoir. We are perhaps ready to see now that those responses relate to the long-standing denial that through the centuries scientists, and often the greatest among them, have been concerned with achieving and safeguarding their priority. The question is, of course: What leads to this uneasiness about acknowledging the drive for priority in science? Why the curious notion that a thirst for significant originality and for having that originality accredited by competent colleagues is depraved--somewhat like a thirst for, say, bourbon and 7-Up? Or, in Freud's self-deprecatory words, that it is an "unworthy and puerile" motive for doing science? In one aspect, the embarrassed attitude of a Darwin or Freud toward his own interest in priority is based upon the implicit assumption that behavior is actuated by a single motive, which can then be appraised as good or bad, as noble or ignoble. It is assumed that the truly dedicated scientist must be moved only by the concern with advancing knowledge. As a result, deep interest in having one's priority recognized is seen as marring nobility of purpose as a scientist. There is, moreover, a germ of psychological truth in the suspicion enveloping the drive for recognition in science. Any extrinsic reward--fame, money, position--is morally ambiguous and potentially subversive of culturally esteemed values. For as rewards are meted out, they can displace the original motive: Concern with recognition can displace concern with advancing knowledge. An excess of incentives can produce distracting conflict. In another aspect, the ambivalence toward priority means that scientists reflect in themselves the ambivalence built into the social institution of science itself. That ambivalence also derives from the mistaken belief that concern with priority must express naked self-interest, that it is altogether self- serving. On the surface, the hunger for recognition appears as mere personal vanity, gener- ated from within and craving satisfaction from without. But when we reach deeper into the institutional complex that gives added edge to that hunger, it turns out to be anything but personal, repeated as it is with slight variation by one scientist after another. Vanity, so called, is then seen as the outer face of the inner need for assurance that one's work really matters, that one has measured up to the hard standards maintained by at least some members of the community of scientists. Sometimes, of course, the desire for recognition is stepped up until it gets out of hand. It becomes a driving lust for acclaim; megalomania replaces the comfort of reassurance. But the extreme case need not be taken for the modal one. In providing apt recognition for accomplishment, the institution of science serves several functions, both for scientists and for maintenance of the institution itself. The community of science provides for the social validation of scientific work through peer assessment. In this respect, it simplifies that famous opening line of Aristotle's Metaphysics: "All men by nature desire to know." Perhaps, but men of science, by culture, desire to know that what they know is really so. The organization of science operates as a system of institutionalized vigilance, involving competitive cooperation. It affords both commitment and reward for finding where others have erred or have stopped before tracking down the implications of their results or have passed over in their work what is there to be seen by the fresh eye of another. In such a system, scientists are at the ready to pick apart and appraise each new claim to knowledge. Only after the originality and consequence of their work have been attested by significant others can scientists feel reasonably confi- dent about it. Deeply felt praise for work well done, moreover, exalts donor and recipient alike; it joins them both in symbolizing the common enterprise. That, in part, expresses the character of competitive cooperation in science. The function of reassurance by recognition has a dependable basis in the social aspects of knowledge. Few scientists have great certainty about the worth of their work. Even that psychological stalwart, T.H. Huxley, seemingly the acme of self-confidence, tells in his diary what it meant to him to be elected to the Royal Society at the age of 26, by far the youngest in his cohort. It provided him, above all, with much needed reassurance that he was on the right track; in his own language, "acknowledgment of the value of what" he had done. And since, like the rest of us, Huxley was occasionally inclined to doubt his own capacities and to think himself a fool, he concluded that "the only use of honors is as an antidote to such fits of `the blue devils.'" The drive for priority is in part an effort to reassure oneself of a capacity for original thought. Thus, rather than being mutually exclusive, as the new mythology of science would have it, joy in discovery and the quest for recognition by scientific peers are stamped out of the same psychological coin. In their conjoint ways, they both express a basic commitment to the value of advancing knowledge. But authentic reassurance can be provided only by the scientists whose judgment one in turn respects. As we sociologists like to put it, we each have our reference groups and individuals, whose opinions of our performance matter. Our peers and superiors in the hierarchy of accomplishment become the significant judges for us. Darwin writing Huxley about the Origin of Species "with awful misgivings" thought that "perhaps I had deluded myself like so many have done, and I then fixed in my mind three judges, on whose decision I determined mentally to abide. The judges were Lyell, Hooker, and yourself." In this, Darwin was replicating the behavior of many another scientist, both before and after him. The astronomer John Flamsteed, before his vendetta with Newton, wrote that "I study not for present applause. Mr. Newton's approbation is more to me than the cry of all the ignorant in the world." In almost the same language, Erwin Schrodinger writes Einstein that "your approval and [Max] Planck's mean more to me than that of half the world." And a Leo Szilard or a Max Delbruck, widely known as exceedingly tough-minded and demanding judges who, all uncompromising, will not relax their standards of judgment even to provide momentary comfort to their associates, are reference figures whose plaudits for work accomplished have a multiplier effect, influencing in turn the judgments of many another scientist. Other strategic facts show the inadequacy of treating an interest in recognition of scientific work as merely an expression of egotism. Very often, the discoverers themselves take no part in arguing their claims to the priority or significance of their contributions. Instead, their friends or other more detached scientists see the assignment of priority as a moral issue not to be scanted. For them the assigning of all credit due is a functional requirement for the institution of science itself. After all, to protect the priority of another is only to act in accord with the norm, which has been gathering force since the time of Francis Bacon, that requires scientists to acknowledge their indebtedness to the antecedent work of others. As Peter Kapitza says of his master, "If anybody in publishing his work forgot to mention that the given idea was not his own, [Ernest] Rutherford immediately objected. He saw to it in every possible way that ... true priority be maintained." Or, to take perhaps the most momentous instance in our day, there is Niels Bohr, agitated by the thought that Lise Meitner and Otto Hahn--and, for that matter, Otto Frisch and Fritz Strassmann--might have their priority in the splitting of the atom lost to view in the avalanche of publicity given the Columbia University experiments, going to immense pains to set the record straight (just as he was later to devote himself to the task of getting governments, and physicists too, to consider the human consequences of nuclear weapons). Erwin Chargaff is correct, I believe, in suggesting that the Watson memoir "may contribute to the much-needed demythologizing of modern science." But as I have tried to suggest, to put the accent on "modern science" is only to displace the old myth with a new variant. In noting this, I am scarcely alone. Some practicing scientists, both before and after The Double Helix, have put aside the myth that competition for originality in science is alien to joy in discovery and that the drive for recognition should occasion self-contempt. Hans Selye asks his peers: "Why is everybody so anxious to deny that he works for recognition? . . . All the scientists I know sufficiently well to judge (and I include myself in this group) are extremely anxious to have their work recognized and approved by others. Is it not below the dignity of an objective scientific mind to permit such a distortion of his true motives? Besides, what is there to be ashamed of?" And, as though he were responding to this rhetorical question, P.B. Medawar goes on to argue: "In my opinion the idea that a scientist ought to be indifferent to matters of priority is simply humbug. Scientists are entitled to be proud of their accomplishments, and what accomplishments can they call `theirs' except the things they have done or thought of first? "People who criticize scientists for wanting to enjoy the satisfaction of intellectual ownership are confusing possessiveness with pride of possession."

Scientists' Competitive Behavior Is Not Peculiar To Our Competitive Age

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