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Setting Scientific Agendas

David Goodstein

Science, Truth, and Democracy. Philip Kitcher. xiv + 219 pp. Oxford University Press, 2001. $29.95.

Of what value to scientists is the philosophy of science? It is certainly of value if it causes us to question our basic assumptions, or even to realize under what unstated assumptions we have been operating.

Distinguished philosopher of science Philip Kitcher tells us in Science, Truth, and Democracy that we scientists are realists—that is, we believe that there is a real world out there and that science can figure out how it works. To Kitcher, this is an extreme view, just as unacceptable as its opposite: that there is no such thing as truth, and science is a belief system no better than any other. With some evident trepidation, Kitcher stakes out a position for himself that is closer to the scientist's view than to its opposite. There is a real world out there, he believes, and science is able to discover important truths about it; the key, he thinks, is the word important.

Important to whom, and for what purpose? He argues that there can be no objective, context-free way of deciding. The only reasonable approach, he decides, is to assume that scientific truths are important if their fruits are beneficial. Thus the doing of science for its own sake is not an absolute good but must be judged by the benefits that arise out of it, provided those benefits are distributed fairly and equitably. He concludes that ideally the decisions that set the agenda of science would be made democratically, with the informed collaboration of every segment of society. The elaborate means by which that collaboration would be carried out he calls well-ordered science.

Kitcher likes to argue by setting out polar extremes, deciding that neither can be correct and concluding that the truth must lie somewhere in the middle. This technique makes him seem eminently reasonable at every step, no matter how far off the real axis he leads us. Kitcher contrasts well-ordered science with alternative ways of setting the scientific agenda. At one extreme is what he calls internal elitism, in which scientists make all the decisions about what the agenda should be. In actuality, however, decisions are made by scientists together with a privileged group of outsiders ("paymasters") who have the funds to support research. This (the status quo) Kitcher calls external elitism, which is under constant pressure from scientists who want to convert it to internal elitism.

At the opposite extreme from internal elitism is vulgar democracy, which attempts to satisfy citizen preferences by giving priority to projects that are believed to be favored by a majority of people—an approach with the obvious deficiency that it could result in "a tyranny of the ignorant." The best alternative to either extreme, Kitcher proposes, is enlightened democracy, in which decisions would be made by groups representing every segment of society, after they had been tutored by scientists. This is a condensed version of the more elaborate deliberations of well-ordered science. It is an approach that may seem entirely reasonable to those who have never tried to explain to nonscientists what science is about, as I have spent a lifetime doing.

The issues that seem to motivate Kitcher's arguments are seen most clearly in the biomedical arena (his favorite examples are drawn from genomics). The National Institutes of Health (NIH) habitually expands its budget with the argument that the research it supports benefits the health and well-being of all. (The fact that the NIH budget is many times larger than that of the National Science Foundation is evidence that democracy does have its effect in setting the research agenda.) Kitcher analyzes a 1998 committee report addressing the charge that NIH is more interested in satisfying the curiosity of scientists than in improving patient care. Although the report did call for more public input, it also defended the status quo, saying that NIH has produced an "accumulation of basic knowledge about human biology that is unparalleled in the history of science." Kitcher agrees but points out that NIH has received a level of funding that is also unparalleled in the history of science. Without a control—something the committee members would certainly insist on in their own work—we can't be sure that a different method of setting NIH priorities would not have produced even more beneficial results. But the history of science provides no control.

Of course it is not only biology that bellies up to the public trough with promises to contribute to the public welfare. In order to procure funding to pursue whatever we find interesting, many of us have adopted the embarrassing habit of claiming that our research will produce material benefits. And we have produced the material benefits almost in spite of ourselves. It is true, as Kitcher says, that it would be very difficult to connect the industrial revolution of the 19th century to pure research. But it is not at all difficult to connect the extraordinary prosperity of the 1990s to pure research done decades earlier—much of it, ironically, justified at the time by the Cold War.

Physicist Richard Feynman was disdainful of philosophers of science, but he was nevertheless capable of deep insights. Many years ago, he and I had long discussions of precisely the central question of Kitcher's thesis: What makes something important in science? The context was not how to set national research priorities, but rather a different question that intrigued both of us. Some scientists consistently made important discoveries, while others with equal technical skills were relatively unproductive. Why?

The key, Feynman decided, lay in choosing important problems to work on. An important problem, he believed, is one for which the solution turns out not only to solve the problem at hand but also to shed unexpected new light on the solutions to other problems as well. Feynman's formulation is both enigmatic and elegant. The ability to choose such problems is what we call scientific good taste. Some people have it and others don't. Democracy has nothing to do with it.

Of course, Feynman was the ultimate high priest of science, secure in the unquestioned belief that the pursuit of truth is a good thing. Kitcher says there can be no justification for that unexamined faith. Characteristically rejecting it, together with its polar opposite, he calls for "agnosticism all the way down." What he finally concludes can be summed up crudely as, What good is truth if it can't buy happiness?

Kitcher's book has indeed made me think about my basic assumptions, but it has not made me change them. I remain a flaming realist and an unreconstructed internal elitist, yielding reluctantly to external elitism when I need more funding. Unlike Kitcher, I do not fear the unfettered search for truth. In fact, in considering ways in which our civilization might come to an end, one prominent possibility is that we might stop asking scientific questions because we fear to know the answers.

We don't know in advance what results scientific research will produce. Some scientists have the instinct to ask the most important questions. Our system of decision making, imperfect as it is, does tend to identify those individuals and give them the resources they need. All things considered, I believe that is a better way of governing the business of science than Kitcher's ideal of well-ordered science.—David Goodstein, Physics, California Institute of Technology

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