Why the philosophy of science actually does matter

Biologists, in general, tend to have relatively little interest in the philosophy of science. There is a sound basis for this indifference: the great majority of biologists manage to do perfectly good science without having had much more than a brush, usually as undergraduates, with this branch of philosophy. Furthermore, even well before there was a welldefined academic discipline called the ``philosophy of science'', there were outstanding individuals who did superb scientific work, without benefit of a clearly defined philosophical framework. Darwin, famously, is on record as saying: 1) that he collected facts wholly without preconceptions and 2) that he always looked at facts with some provisional idea of how they might make sense. Clearly, his lack of consistency, or even understanding, about his own way of operating did not prevent him from doing ground-breaking work. It is no wonder, therefore, that many biologists privately regard the chief function of the philosophy of science as something to provide employment to a small number of academics in philosophy departments. Furthermore, recent advances in the ways that molecular biologists gather data seem to threaten a fundamental tenet of the philosophy of science, further diminishing its relevance to the actual practice of science. That tenet is that scientific knowledge is advanced by the testing of hypotheses. The new techniques, which have created veritable oceans of data to swim through, seem to have made hypothesis-testing obsolete; the data, it is thought, can speak for themselves. Indeed, one of the developers of micro-array techniques has been widely quoted as declaring, ``The era of hypothesis-driven research is over. '' In other words, Popperism is pooped-out and induction (the pure gathering of facts and generalization of their meaning without any preconceived notions) is in. On p. 104 of this issue, John Allen challenges that notion. He points out that any assessment or interpretation of significance involves an hypothesis and that investigation of any correlation turned up by the new methods involves hypothesis-testing. Imagine a typical microarray experiment that is used to track changes in gene expression during the course of a particular developmental change in a certain organism. Let us say that you identify 1053 genes whose mRNA levels go up, 393 that go down, and 4126 that stay the same. Which ones do you concentrate on? The easy decision is to ignore the 4126 that stay the same. Yet, that involves an assumption, in fact an hypothesis; there may be some genes, even a large number, in that group, that play a role in the developmental change of interest, although their expression rates are unaltered. But what about the ones that do change? Which ones do you investigate first? Those that go up, those that go down, those that have the largest changes, those that carry one sequence motif vs. another? Each of those choices involves an hypothesis about what is important. Rather like M. Jourdain in Moliere's Le Bourgeois Gentilhomme, who discovers, to his astonishment, that he has been speaking prose all his life, the scientist doing a microarray experiment is continually hypothesis-testing, whether or not he/she thinks of it that way. This hypothesis-testing may not be hard Popperian, since many of these experiments seek confirmation rather than falsification, but they are hypotheses, nevertheless. The choice is not whether your research will or will not be guided by hypotheses but whether the hypotheses being tested are consciously chosen or whether they are dictated by hunch and fashion. Yet, if the detailed work of much (indeed, all) of molecular biology is based on philosophical tenets, even when not overtly recognized as such, what about the larger picture? Does the philosophy of science come into the question of how one chooses one's scientific goals or major projects in the first place? Surprisingly, here, too, the answer is ``yes''. Three years ago, the Novartis Foundation (formerly the Ciba Foundation) held a symposium on the subject of reductionism in science. Its title was ``The limits of reductionism'' and the central issue addressed was whether the properties of complex systems can be deduced or reconstructed from detailed knowledge of the properties of their constituents and the direct interactions of those constituents. This is the sort of philosophical issue that many biologists will respond to with an upward roll of the eyes and/or a shrug. Yet, as one of the discussants pointed out succinctly, the issue of whether reductionist approaches are the sole route to understanding complex systems is really a question about what gets funded, hence about who gets funded. If, for instance, you are interested in some aspect of the operation of the CNS, do you take an exclusively hard core reductionist approach, and concentrate on identifying all the genes and gene products that might be involved in the relevant areas of the brain? If so, your tacit assumption is that the properties of the system will become apparent from their study. Or, do you characterize the systems properties first, to try to obtain clues as to which neural processes, regions and (ultimately) molecules, might be important? Most researchers would probably respond to this choice with, ``you need both sorts of approach''. But, even accepting that, how do you apportion the money to them? Do you give 99% to reductionist strategies and 1% to system