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Research and
the culture of instrumentalism

Scientists have always been great improvisers. But today's institutional pressures too often force them to keep their eyes on the score. Drawing on his own creative experience and the wisdom of his Columbia mentor, a Nobel Prize winner offers his suggestions for a new arrangement


TODAY'S SCIENTIFIC CULTURE often overlooks a principle that is both paradox and common sense: You rarely find the most important things by deliberately looking for them. The obvious remedy would be to foster serendipity, but serendipity means more than the good luck of accidental discovery. As Louis Pasteur said, "Chance favors the prepared mind," and the prepared mind requires unfettered opportunity to recognize and follow unplanned paths. Even if we set a goal and succeed in accomplishing it, that's not the way we work revolutions. But when we pursue our passion to master what was once unknowable, we move from a plodding struggle with nature to an ongoing, enlightening conversation. We also then stumble upon the kind of advances that repeatedly justify society's great investment in science.

Ryan took a callow underclassman
from Washington Heights and turned me
into a scientist; he took me seriously enough
to discipline my thinking

In my own life as a researcher I've had the good fortune to work with some of the most inquisitive minds in biology, learning as they learn at the leading edge of their discipline. I can't overestimate the value of guidance by those who combine curiosity with a generous and patient spirit. Foremost among these was my mentor at Columbia College, Francis J. Ryan. Professor Ryan took a callow underclassman from Washington Heights, brash and argumentative as precocious students often are, and turned me into a scientist; he took me seriously enough to discipline my thinking, which was exactly what I needed right then. He guided me through an unusual course of study, from graduate-level zoology courses during my freshman and sophomore years to doctoral work at both Columbia and Yale, transferring new methods from the molecular genetics of the bread mold Neurospora to the study of the bacterium Escherichia coli. Working with the botanical material Neurospora in a zoological department-Columbia's biological science departments were not yet unified-did get Ryan into some difficulties, but he characteristically preferred to follow the path of free inquiry across whatever borders it might traverse, institutional or Linnaean.

When I made the discovery that led to both my doctorate and my later Nobel Prize, the finding that a certain bacterial strain exhibited conjugal behavior and exchanged genetic material, it was on a research leave and Jane Coffin Childs Fellowship that Francis had helped arrange, letting me set aside my medical studies at P&S to work at Yale with his own mentor Edward Tatum. Encouraging my microbiologic avocation was a gamble, given what was believed about bacterial genetics at the time. But Francis, whose own career had taken a similar route (he came to Columbia as a premedical student but ended up detouring into research and took his doctorate in zoology), understood that long shots sometimes pay off spectacularly.

Looking back at this exciting period across some 50 years, I am struck by the willingness on the part of both Francis Ryan and, eventually, the system as a whole to make room for speculations that went contrary to the common wisdom of the day. The prevailing paradigm, in which bacteria were thought to be "schizomycetes" or asexual, primitive plants, predicted that nothing would come of our investigation; indeed, had we not fortuitously used the unique K-12 strain of the organism, nothing would have. No immediate applications followed from our work. One might wonder whether reviewers of project grant proposals in today's impatient mood would find much promise in the hypothesis that a mutant strain of E. coli has a sex life. It's not difficult to imagine such studies attracting the kind of unwanted attention reflected by Sen. William Proxmire's "Golden Fleece" awards or the anti-intellectual mockery that currently crowds the radio channels.

Yet our forays into bacterial genetics, along with the work of Oswald Avery's group at the Rockefeller Institute, Watson and Crick at Cambridge, and many others, helped clarify our basic understanding of the role of DNA in evolutionary adaptation, along with laying the foundation for today's molecular biology and its applications in biotechnology. The practical benefits include not only new medicines but a detailed understanding of how viruses and microorganisms perpetuate and defend themselves. Our species' continued well-being is threatened by exotic new plagues, just as current best sellers dramatize; we had better know as much as we can about the causative agents. The life at stake is your own.

Not once during my formative years in biomedical science did I imagine there might be a divergence between the path my mind was taking-the path of the basic researcher, asking deep questions of nature-and the path society wanted it to take. The debate that percolates in Washington these days about science and its value to society, however, appears to confuse scientific purpose as I understand it with scientific outcomes. It is critical that institutions like my alma mater Columbia and my professional center Rockefeller University not only carry forward the nation's research agenda but make their voices heard on ways to reconcile this divergence.

Wartime research funding in the 1940s and continuing support in the postwar years helped sustain my work and that of countless others. There is no doubt that the Allies' victory in World War II was due in large part to America's ability to galvanize that community behind the war effort, as represented by radar, not to mention the atomic bomb. These awesome achievements represented a convergence of basic research and specific military applications, driven by unprecedented national investment. "Basic" and "applied" science needn't be miles apart; after all, the bomb was fabricated barely 12 years after the discovery of the neutron.

The shock of Sputnik in 1957 reinvigorated a national consensus that basic research was a net social good. The continuing investment that follows from this consensus has yielded technological innovations major and minor: computers, lasers, vaccines, biotechnology, superconductors, eventually interactive video on demand. Certainly there will be others we can't predict. The pattern of serendipity holds for applications as well as for basic knowledge.

Somewhere between the moon landing and the end of the Cold War, however, the cultural consensus began to splinter. Skepticism did not set in simply because the need for military hardware declined; rather, for at least a decade before 1990, policy-makers and citizens had increasingly questioned whether particular projects produced a demonstrable public benefit. Both Sen. Proxmire's awards and the jeers of talk radio's opinioneers reflect a changing perception of much university-based research as frivolous, a counting of mythical angels on the heads of mythical pins. Presuming an absolute dichotomy between basic and applied science, critics equate the former with angel counting, whereas the latter produces things society can use. To a growing number of policy-makers supervising the public purse, only the latter deserves the help of hard-working taxpayers. Let the angel counters find support elsewhere.

Instrumentalism, or scientific purpose driven to meet specific needs, seems increasingly to be the underlying rationale for our investment in research. The instrumental payoffs from basic science have often bridged the gap between angel counters and bean counters; indeed, they have bridged it so effectively that the research university has become big business, largely funded by the federal government and inevitably entangled with politics. But the stresses of that entanglement lately are revealing a fundamental schism within the culture of science in the United States.

One might wonder whether reviewers of project proposals in today's impatient mood would find much promise in the hypothesis that a mutant strain of E. coli has a sex life

As persuasive as the instrumental argument is, I have serious qualms about accepting it as the sole moral basis for the pursuit of science. Certainly, I do not eschew the practical fruits, but I recoil at the corruption of academic values--particularly the threat to creativity--that follows from a purely instrumental approach. In place of the ideal of a university as a community of scholars who explicate a method of inquiry, discovery, verification, and validation, we see a division of loyalties in which all but a few researchers are tethered to the short-term project system, unable to look beyond the imperative of grant renewal. In place of responsible institutional oversight, we see the encroachment of a grantsmanship culture that often allocates rewards to those skilled at manipulating the system, independently of the merit of their ideas. And in place of skeptical questioning and constructive revision of scientists' ideas by the community at large, we are increasingly seeing collective technophobia, a reflexive distrust of science and scientists that borders on Luddite nihilism.

These structural frictions and cultural contradictions have predictable ill effects. Most damaging, in the long run, is that the constraints of a research career are driving gifted young minds away. Strong students are turning from science toward the safer harbors of medical practice, law, or business; it is not only those impatient with non-instrumental (or even instrumental) goals who follow lucrative incentives away from the lab, but also those simply carrying the burden of educational debt. The demands on the scientific personality are already high enough; let's not complicate them with gratuitous stresses.

More glaring are the loudly publicized allegations and facts of fraud, which may reflect a milieu of competitive careerism but nonetheless undercut the moral basis of science. From a purely instrumental perspective, fraud costs very little in authentic scientific output compared to sheer sloppiness and incompetence in experimental design. But fraud is a moral outrage, perhaps another symptom of a system that has grown materialistic and unimaginably vicious.

In the face of these problems, not to mention financial pressures, it is unsurprising that some have called for drastic, damaging cuts. But it makes little sense to reduce the scope of our science and technology when we have not exhausted the possibilities of constructive reform in the federal-university relationship.

To strengthen the culture of science by changing its structures, I propose four reforms:

RECOGNIZE that a research university is a host and enabler for research, not a primary fount for resources. Suggestions that "the institution should pay for X" are unhelpful without informed mandates about sources to tap. Ad hoc demands by distant agencies that will not share responsibility hardly constitute sound management. Neither does enmeshing faculty in administrivia, which they rarely understand in detail.

EMPHASIZE the creativity of investigators, not the substance of proposals. Research is by definition a plunge into the unknown, requiring talents for improvisation. Innovative minds should not have to bootleg their best ideas under the cover of sure-thing applications. The implication that an investigator should demonstrate a specific, achievable goal beforehand flies in the face of the history of scientific progress. About the most important discoveries, we are always too ignorant to make predictions.

LENGTHEN the period of grant awards. One fell swoop of administrative fiat, extending the period from 1-2 years to 5-7 years, would reduce the intolerable workload on both reviewers and investigators. Short-term awards conduce to micromanagement of others' work, misunderstanding between applicants and reviewers, and destructive career cycles in which encouragement alternates with distress. The grant system should attune itself to the rhythms of a scientific life, not vice versa.

SHARE responsibility. Today's project funding system encourages fragmentation, when what we need is interdisciplinary vision by department chairs, deans, provosts, and presidents alike. Leaders who are cognitively engaged with the work they oversee can restore the loyalties that properly extend to one's colleagues and institution. This can only strengthen the research community, internally and in the eyes of the public.

At the heart of the research enterprise lies a paradox that Francis Ryan understood well: The best way to achieve scientific progress is to resist the temptation to control it. "The mind goes antagonizing on," as Emerson wrote in a meditation on the unpredictability of genius(1); the most productive movements of mind are those unencumbered by premature expectation of the rewards they will yield. Society may never again recover a consensus that science and technology deliver an unalloyed boon to humankind; one of science's most spectacular successes, the atomic bomb, also ensured that the scientist's work will always be complicated by grave questions of conscience. But exercising an active conscience does not mean dispensing with the freedom to inquire or the patience to let inquiry work in its own mysterious ways.

  1. Emerson, Ralph Waldo, "Experience," from Essays: Second Series, reprinted in Essays and Lectures (Porte, Joel, ed.). New York: Library of America, 1983, p. 483.

Prof. Francis Ryan "dines" in the lab: photo courtesy Columbiana Archive.
Prof. Lederberg: photos by Lena Lakoma.

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