In this outline of Hull's ideas, I have not yet mentioned one of his main arguments. Hull tries to describe scientific change as an evolutionary process, in a sense derived from biology. Science changes via processes of variation and selection, just as biological populations do. Individual ideas in science are replicated in something like the way that genes are. And the different rates with which ideas are replicated are consequences of their manifestations in the brains and the public representational systems (books, journals, computers) of the scientific community. Scientific change is a process in which some ideas outcompete others in a struggle for replication.
The idea of understanding scientific change via an explicit analogy with biological processes of variation and selection has been tried out by a number of writers (Toulmin 197z; Campbell 1974; Dennett 1995). As we saw in chapter 4, Popper's view of science also has an analogy with evolution by natural selection, although Popper did not start out with this analogy in mind.
Though the analogy between science and Darwinian evolution is something that people keep coming back to, the analogy has not yielded a lot of new insights so far. We find the same result in many other attempts to describe cultural change as an evolutionary system; a wide variety of processes can be described in a way that borrows from evolutionary biology, but usually this exercise does not teach us anything about those cultural processes that we did not know before. Biological populations have special features that make the abstract concepts of evolutionary theory helpful in trying to understand them. Other systems, which lack these features, can be described in evolutionary terms with a bit of shoehorning, but we do not seem to gain much from doing so.
That does not keep the analogy between evolution and scientific change from being an interesting one. The analogy can be interesting without being a basis for a new theory of science.
11.2 Kitcher and the Division of Scientific Labor
I move to a second example of naturalistic work on the social structure of science, this one from the work of Philip Kircher.
In chapter 7 I discussed Lakatos's and Laudan's views about competition between research programs. Both presented a picture of science based on competition between teams of workers developing rival theories and perhaps defending rival methods. This picture seems to cover some parts of science rather well. Both Lakatos and Laudan were interested in giving normative rules for scientific behavior in this situation. But as I said back then, there is a gap in their treatment of the issue. They were thinking of rational choices by individuals. We can also look at the situation from the point of view of the scientific community, and we can ask, What is the best distribution of workers across rival research programs, for the community as a whole?
Kircher takes up this issue in detail (199o, 1993). He starts by asking this question: suppose you ruled science "from above" and had to allocate resources to rival research programs. In a particular scientific field, you find two different approaches being taken to the same problem. Research program i looks more promising than research program z, but no one knows which approach will ultimately work. However, it is clear that either one will succeed while the other fails, or both will fail. How should you allocate resources, to maximize the chance that the scientific problem will be solved?
The answer will depend on the details of the case, obviously. But it seems clear that in a wide variety of situations, the best approach will not be to allocate all resources to one option and none to the other. Some degree of "bet-hedging" will often be advisable, even in cases where one program is obviously more promising than the other. A wise "ruler of science" would often allocate most of the resources to the better research program but some resources to the alternative.
To say more than this, we need to represent the situation mathematically, and that is what Kircher does. The crucial features of the situation will be the degree to which one program is more promising than the other and the mathematical functions that describe how each research program responds to the addition of more resources. Here is a simple case. Suppose that both research programs become more and more likely to succeed as more workers are added to them, but in both cases there is a "decreasing marginal return." As more workers are added to a program, each additional worker makes less and less difference to the chances of success. We can then see why an optimal allocation of resources will often not put every worker on one program. After a certain point, adding more workers to a program has almost no effect, and these people would be better put to work on the alternative. Unless the total pool of workers is small and the overall difference in promise is big, the best distribution of workers will allocate some to one program and some to the other.
That is what we would want if the allocation of resources could be controlled from above. But of course, this is not how things usually work. Now suppose that individual scientists are making their own choices about which program to work on. The next question Kircher asks is, What kind of individual reward system in science will tend to produce distributions of workers that benefit science as a whole? What kind of reward system will tend to produce the same distribution of workers that the "ruler from above" would want?
One option that would not work well would be to give a fixed reward to everyone who works on the program that eventually succeeds, regardless of how many workers there are. That system would induce everyone to choose the more promising program, and the community would have all its eggs in one basket. Another approach would be to reward individuals for making choices that produce the maximum benefit in terms of the overall chance that the community will solve the problem. This would work in principle, but it does not seem a realistic reward system for actual scientific communities. So here is a third option: we reward only the individuals who work on the research program that succeeds, but we divide the "pie" equally between all the workers who chose that program. So the reward that an individual gets will depend not just on their own choice but on how many other individuals chose the same program.
This third reward system, Kircher argues, will produce a good distribution of workers across the two options. We can see why that is. Once one research program becomes crowded, an individual has little incentive to join that program because, if it does pay off, the pie is being divided among too many people. Although the other program is less likely to succeed, if it does succeed, there will be fewer workers sharing the reward. So an individual who wants to maximize his or her "expected payoff" will often have reason to choose the less promising program. In this way, selfish individual choices will produce a good outcome for the whole community. And Kircher suggests that this reward system is fairly close (with simplifications) to what we actually find in science. The "pie" here is not cash but prestige.
Kitcher's story has a definite "invisible hand" structure. We have selfish individual behaviors combining to produce a good outcome for the com munity. This outcome might be one that the individuals are uninterested in or even unaware of.
Kitcher's work has recently been followed up by Michael Strevens (2oo3 ). Strevens shows that Kircher was too optimistic about the reward system in which a fixed pie is shared equally by all workers on a successful program. Although this reward scheme will tend to produce a fairly good distribution of workers from the point of view of the community, it often will not produce the best distribution. Suppose you are making the choice of which program to join. There are cases where you will do best to join the more promising program even though your joining makes little or no difference to its chance of success. Others have given the program a good chance of success, and your joining gives you a good chance of an equal share of the pie, though your efforts would have been more productive if you had joined the alternative program. Had you joined the alternative, you could have made a real difference to the community's overall chance of solving the problem. So a kind of "free riding" is encouraged in Kitcher's reward scheme.
Strevens argues that another reward scheme is both better for the community and closer to the actu
al situation in science. This scheme allocates rewards to an individual that are proportional to the contribution he makes to the particular research program that he joins. The payoff is given only if a research program solves the scientific problem, and the pie is shared unequally among those working on the successful program. Workers who joined early and made a big difference to the program's chance of success get more than workers who joined late and made little difference.
There is obviously a great deal more detail that could be added here; I have just introduced the simplest part of a complicated model. The overall picture is clear, though. Hull, Kitcher, Strevens, and others are looking at the relationship between individual incentive and communitylevel success in science. The argument-made most bluntly by Hull but endorsed by others-is that science has hit on a particularly effective way of coordinating individual energies to yield good outcomes for the community as a whole.
11.3 Social Structure and Empiricism
At the end of the previous chapter, I began to sketch a version of empiricism based on a naturalistic approach to philosophy. Science attempts to exploit the contact with the world that humans have via experience, using this contact to explore and assess hypotheses about the world. In this sense, we might think of science as a strategy for answering questions and working out what to believe. To a very limited extent, this strategy can be followed by a lone individual, but what results is something that has few of the distinctive features of science. The power of science is seen in the cumulative and coordinated nature of scientific work; each generation in science builds on the work of workers who came before, and each generation organizes its energies via collaboration and public discussion. This social organization permits the scientific strategy to function at the level of social groups; the dialogue between the speculative voice and the critical voice can literally be a dialogue, rather than something internalized in the mind-set of the individual scientist. These social groups can include some individuals who are not especially open-minded-who are very wedded to their own ideasprovided that the group as a whole retains flexibility and responsiveness to evidence.
So how do we get a community of individuals to behave in this sort of way? We need a suitable reward system and also various external supports. Some of what is needed is obvious; scientists need to be able to make a living, unless we intend to leave it all to rich amateurs. The society as a whole must allow questioning and open-ended inquiry. Though these factors are obvious, other needs are probably more subtle. The work of people like Merton and Hull suggests that science may need a specific kind of internal culture and reward system; the delicate balance between competition and cooperation is not easily achieved. But there are many unanswered questions here. Might science work just as well, or better, with a slightly different reward system from what we find today? Do we really need the intense and often egoistic competition found in the science of Western marketbased societies? Those who like competitive, individualist societies will be inclined to say yes; they will think that nothing else can generate the precious patterns of scientific social behavior. Those who dislike individualism and competition, who prefer a more communitarian or socialist society, might say no; they will hope that we could do as well or better with a different reward system and a less competitive atmosphere.
This is a point where some feminist discussions of science are relevant. Some feminists hold that the competitive and individualist culture of science is more in tune with the temperaments of men than of women. This affects the ability of many women to flourish within the culture of mainstream science. If it is real, this exclusion may have epistemological consequences. Suppose it is also true that women bring a different "style" of thought and investigation to science and that science benefits from diversity of this kind. In that case (and there are a lot of "ifs" here), the competitive culture of science will tend to produce subtle kinds of uniformity in scientific thinking and will reduce the frequency of a valuable kind of input into scientific discussion.
So we see that there are several ways in which Hull's blunt assertion of the harmony between individual-level and grouplevel benefit in science might be overstated. One of Hull's own examples is interesting here. Hull discusses, and extends, work by sociologists on the temperament and leadership styles of successful scientists. The data suggest that an aggressive faith in one's own ideas, the pushiness of a "true believer," can be useful in at least some fields. Hull refers to a sociological study in which a detailed survey of students and colleagues was used to investigate the temperaments of some famous twentiethcentury psychologists in the United States. One contrast is especially interesting, that between B. F. Skinner and E. C. Tolman. Both Skinner and Tolman were in the "behaviorist" tradition in psychology; they wanted psychology to be experimental, quantitative, and closely focused on behavior. But Skinner's version of this approach was almost absurdly strict, while Tolman's was more flexible. Tolman was also a modest, open-minded, considerate sort of person; Skinner was dogmatic and pushy. And Skinner, with his crusading zeal, had much more influence than Tolman. We cannot know for sure what role temperament had in explaining this difference in success, of course, but the data are suggestive (and Hull found similar results in a smaller study of his own).
So suppose that pushiness and zeal work well for individuals. Does this tend to result in good outcomes for science? In this case, a good argument could be made for the opposite view. I conjecture, and many psychologists would agree, that if Tolman had dominated mid-twentieth-century psychology rather than Skinner, it would have been far better for the field. (Some of Tolman's ideas are currently being revived [Roberts 1998].) I suspect that Hull might reply that the possible problems raised by the feminist objection just above, and those illustrated by the case of Skinner and Tolman, are a small price to pay for the benefits gained from the present balance of competition and cooperation in science.
We must also bear in mind that the internal culture of science is not something fixed and unchangeable. The ideas of people like Merton, Kuhn, Hull, and Kircher might describe science from the seventeenth to the twentieth centuries, but change may well be in the air (Ziman zooo). Scientists have usually not hoped to become rich through their work; recognition, especially by their peers, has been an alternative form of reward. But a number of commentators have noted that big financial rewards have now started to become a far more visible feature of the life of the scientist, especially in areas like biotechnology. Kuhn warned that the insulation of science from pushes and pulls deriving from external political and economic life was a key source of science's strength. We do not know how fragile the social structure of science might be.
In any case, this chapter and the previous one have introduced some of the main themes in naturalistic philosophy of science. Naturalists hope that by combining philosophical analysis with input from other disciplines, we will eventually get a complete picture of how science works and what sort of connection it gives us to the world. This last issue-the connection that science gives us to the real world we inhabit-has often been mishandled by sociology of science and Science Studies. That is the topic of the next chapter.
Further Reading
For assessments of Hull's theory of science, see the reviews in Biology and Philosophy, volume 3 (1988). Also see Sterelny 1994.
Kitcher's main work here is The Advancement of Science (1993). The model discussed in this chapter is presented in a simpler form in Kircher 1990. Solomon (zoos) defends a "social empiricism" in detail, with many examples from the history of science.
For a more general discussion of social structure and epistemology, see Goldman 1999. Downes (1993) argues that some naturalists do not take the social nature of science seriously enough. Sulloway 1996 is a very adventurous discussion of the role of personality and temperament in scientific revolutions.
12.1 Strange Debates
What does science try to describe? The world, of course. Which world is that? Our world, the world we all live in and int
eract with. Unless we have made some very surprising mistakes in our current science, the world we now live in is a world of electrons, chemical elements, and genes, among other things. Was the world of one thousand years ago a world of electrons, chemical elements, and genes? Yes, although nobody knew it back then.
But the concept of an electron is the product of debates and experiments that took place in a specific historical context. If someone said the word "electron" in Iooo A.D., it would have meant nothing-or at least certainly not what it means now. So how can we say that the world of iooo A.D. was a world of electrons? We cannot; we must instead regard the existence of electrons as dependent on our conceptualization of the world.
Those two paragraphs summarize one part of an argument about science that has gone on constantly for the last fifty years, and which stretches much deeper into the history of philosophy. For some people, the claims made in the first paragraph are so obvious that only a tremendously confused person could deny them. The world is one thing, and our ideas about it are another! For other people, the arguments in the second paragraph show that there is something badly wrong with the simple-looking claims in the first paragraph. The idea that our theories describe a real world that exists wholly independently of thought and perception is a mistake, a naive philosophical view linked to other mistakes about the history of science and the place of science in society.
These problems have arisen several times in this book. In chapter 6 we looked at Kuhns claim that when paradigms change, the world changes too. In chapter 8 we found Latour suggesting that nature is the "product" of the settlement of scientific controversy. I criticized those claims, but now it is time to give a more detailed account of how theory and reality are connected.
Theory and Reality Page 24