I will make one last point before leaving Lakatos. In the last few chapters, I have contrasted Popper, who called for permanent open-mindedness and criticism, with Kuhn, who endorsed a tenacious commitment to the basic ideas of a paradigm. This is a standard way of marking a fundamental disagreement between Kuhn and Popper. There is a bit more complexity here, however. Lakatos, as I said, saw many of his ideas as implicit in Popper. And we can indeed find passages in Popper where he accepts that theories should not be discarded at the first sign of trouble but, instead, should be protected initially to see if they can overcome their problems (Popper 1963, 49; 1970, 55). So is there really no difference, or much less difference, between Popper and Kuhn on this point? Has Popper retreated from one of his most basic ideas? Not really. When Popper came to directly confront Kuhns arguments on this issue (1970), he did not choose to blur the difference between his view and Kuhns. He said that Kuhnian normal science does sometimes exist, but it was not nearly as common as Kuhn said. And more importantly, he regarded it as a bad thing, which should not be encouraged.
7.3 Laudan and Research Traditions
In an interesting book called Progress and Its Problems (11977), Larry Laudan developed a view that is similar to Lakatos's in basic structure but which is far superior. Like Lakatos, Laudan thought that Kuhn had described science as an irrational process, as a process in which scientific decisionmaking is "basically a political and propagandistic affair" (1977, 4). This reading of Kuhn (I say yet again) is inaccurate. But Laudan also recognized the power of Kuhn's discussions of historical cases. Like Lakatos, Laudan wanted to develop a view in which paradigm-like entities could coexist and compete in a scientific field. He gave many cases from the history of science to motivate this picture. So we are heading toward the idea of a research program. But in an understandable piece of product differentiation, Laudan called the large-scale units of scientific work "research traditions" rather than research programs.
The difference between Laudan and Lakatos is not just terminological. Laudan's description of research traditions makes more sense than Lakatos's account. Lakatos saw the sequence of theories within a research program as linked very closely by logic; each new theory was supposed to have a broader domain of application than its predecessor in that research program. And for Lakatos, the hard core never changes. For Laudan, the theories grouped within research traditions are more loosely related. There can be some movement of ideas in and out of the hard core. Moreover, for Laudan there is nothing unusual or bad about a later theory covering less territory than an earlier one; sometimes a retreat is necessary. For Laudan, theories can also break away from one research tradition and be absorbed by others. For example, the early thermodynamic ideas of Sadi Carnot were developed within a research tradition that saw heat as a fluid ("caloric"), but these ideas were taken over in time by a rival research tradition that saw heat as the motion of matter.
Another key innovation in Laudan's account is his distinction between the acceptance and the pursuit of theories.
The philosophies discussed here so far have tended to recognize just one kind of attitude that scientists can have to theories. Usually the attitude of a scientist to a theory has been treated as something like belief. Of course, belief can come in degrees; there are cautiously held and firmly held beliefs. Scientists will often-and should often-have only a cautious belief. But still the idea here is that there is one basic kind of attitude-belief or something like it-though it comes in degrees. Laudan argued that there are two different kinds of attitudes to theories and research traditions found in science, acceptance and pursuit. Acceptance is close to belief; to accept something is to treat it as true. But pursuit is different. It involves deciding to work with an idea, and explore it, for reasons other than confidence that the idea is likely to be true. Crucially, it can be reasonable to pursue an idea that one definitely does not accept. Someone might have reason to believe that if the idea was true, it would be of huge importance and the payoff from working on it would be high. Someone might think that although an idea is not likely to be true, it should be explored, and that she or he is the person best equipped to do so. There is a whole constellation of different reasons that a person might have for working with a scientific idea.
Laudan built the distinction between acceptance and pursuit into his account of rational decisionmaking in science. He was able to give some fairly sharp rules where Lakatos had not. For Laudan, it is always rational to pursue the research tradition that has the highest current rate of progress in problemsolving (1977, III). But that does not mean one should accept the basic ideas of that research tradition. The acceptability of theories and ideas is measured by their present overall level of problemsolving power, not by the rate of change. We should accept (perhaps cautiously) the theories that have the highest level of problemsolving power. So a scientist might be inclined to accept the ideas in a mainstream research tradition but work on a more marginal research tradition that has a spectacular rate of progress. For Laudan that decision would be a rational one.
With any rule like this, it will be possible to think of cases where the rule might lead a person astray. What if a research tradition has a low rate of progress right now, but there is good reason to think it might take off very soon? This is the kind of possibility that made Lakatos hesitate. Laudan clearly hoped that the distinction between acceptance and pursuit would help with this kind of problem, and so it does. But he does not try to lay down rules that will deal with every possible situation, including all the various kinds of bad luck. Here we run into a general problem about the aims of philosophy of science; it is very unclear what kinds of principles a philosophy of science should be looking for. Some think that looking for rules of procedure, even sophisticated ones like Laudan's, is just a mistake. But it is fair to say that Laudan was able to give quite an impressive normative theory of science using the idea of competition between research traditions.
Laudan's theory was impressive, but here is an interesting gap in both theories discussed in this chapter that some readers may have picked up on already. Both Lakatos and Laudan were interested in the situation where a scientist is looking out over a range of research programs in a field and deciding which one to join. But here is a question that neither of them seemed to ask: does the answer depend on how many people are already working in a given research program? Both Lakatos and Laudan seemed to think that it would be fine for their theories to direct everyone to work on the same research program, if it was far superior to the others. But perhaps that is a mistake. Science might be better served by some kind of mechanism in which the field hedges its bets. That suggests a whole different question that might be addressed by the philosophy of science: what is the best distribution of workers across a range of research programs?
There are two different ways of approaching this new question. One way is to look at individual choices. Does it make sense for me to work on research program i rather than research program z, given the way people are already distributed across the two programs? Is research program i overcrowded? Perhaps Lakatos and Laudan thought this question was not relevant to their project because it seems to require introducing selfish goals into the picture. But we can also approach the issue another way. We can ask, Which distribution of people across rival research programs is best for science?
Kuhn, interestingly, was aware of this issue, especially in his work after Structure (e.g., 1970). This is ironic because Kuhn did not think that ongoing competition between paradigms was usually found in science. But Kuhn did say that one of the strengths of science lay in its ability to distribute risk by having different scientists make different choices, especially during crises. Lakatos and Laudan were in a good position to make a really thorough investigation of this issue, but they did not (see also Musgrave 1976). It was not until more recently that this question was brought into sharp philosophical focus. We will take up the issue in detail in chapter 1I.
7.4 Anything Goes
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Now we turn to Paul Feyerabend, the most controversial and adventurous figure in the post-Kuhn debates. Feyerabend, like many key figures in this book, was born in Austria. He fought in the German infantry during World War II and was wounded. He switched from science to philosophy after the war and eventually made his way to the University of California at Berkeley, where he taught for most of his career. Feyerabend was initially influenced by Popper, with whom he worked for a year in the 19 5os. But by the early 196os, he was moving toward the adventurous views for which he became famous. He and Kuhn influenced each other significantly. (In dis cussing Feyerabend after Lakatos and Laudan, I am departing from the chronological organization of this book).
So what were his notorious ideas? A two-word summary gets us started: anything goes. Feyerabend's most famous work was his 1975 book Against Method. Here he argued for "epistemological anarchism." The epistemological anarchist is opposed to all systems of rules and constraints in science. Great scientists are opportunistic and creative, willing to make use of any available technique for discovery and persuasion. Any attempt to establish rules of method in science will result only in a straitjacketing of this creativity. We see this, Feyerabend said, when we look at the history of science. Great scientists have always been willing to break even the most basic methodological rules that philosophers might try to lay down. The only rule that we can be sure will not impede imagination and progress is this: anything goes.
In defending his position, Feyerabend made use of a range of ideas about scientific language and the psychology of observation. Like Kuhn, he thought that rival scientific theories are often linguistically incommensurable (section 6.3 above). He argued that observations in science are contaminated with theoretical assumptions and hence cannot be considered a neutral test of theory. These arguments were based on speculative ideas about scientific language, and they are not very convincing. His more interesting arguments are of two kinds. These involve both the history of science and a direct confrontation of some hard questions about how science relates to freedom and human well-being.
Before launching into this unruly menagerie of ideas, we need to keep in mind a warning that Feyerabend gave at the start of Against Method. He said that the reader should not interpret the arguments in the book as expressing Feyerabend's "deep convictions." Instead, they "merely show how easy it is to lead people by the nose in a rational way" (197 5, 3 2). The epistemological anarchist is like an "undercover agent" who uses reason in order to destabilize it. Again we are being told by an author not to trust what we are reading. It is hard to know what to make of this, but I think it is possible to sort through Feyerabend's claims and distinguish some that do represent his "deep convictions." Feyerabend's deepest conviction was that science is an aspect of human creativity. Scientific ideas and scientific change are to be assessed in those terms.
In his article for the Routledge Encyclopedia of Philosophy (1998), Michael Williams suggests that we think of Feyerabend as a late representative of an old skeptical tradition, represented by Sextus Empiricus and Montaigne, in which the skeptic "explores and counterposes all manner of competing ideas without regarding any as definitely established." This is a useful comparison, but it is only part of the story. To capture the other part, we might compare Feyerabend to Oscar Wilde, the nineteenthcentury Irish playwright, novelist, and poet who was imprisoned in England for homosexual behavior. Wilde is someone who liked to express strange, paradoxical claims about knowledge and ideas ("I can believe anything so long as it's incredible"). But behind the paradoxes there was a definite message. For Wilde, the most important kind of assessment of ideas is aesthetic assessment. A book or an idea might look immoral or blasphemous, but if it is beautiful, then it is worthwhile. Other standards-moral, religious, logical-should never be allowed to get in the way of the free development of art. This, I suggest, is close to Feyerabend's view; what is important in all intellectual work, including science, is the free development of creativity and imagination. Nothing should be allowed to interfere with this.
Feyerabend's focus on values and creativity guided his readings of others. His paper "Consolations for the Specialist" (1970) shows him to be one of the most perceptive critics of Kuhn. Most philosophers of science found an alarming disorder in Kuhns view of science. Feyerabend found the opposite: an incitement for scientists to become orderly and mechanical. Feyerabend saw Kuhn as glorifying the mind-numbing routine of normal science and the rigid education that Kuhn thought produced a good normal scientist. He saw Kuhn as encouraging the worst trends in twentiethcentury science toward professionalization, narrowmindedness, and exclusion of unorthodox ideas.
Feyerabend recognized the "invisible hand" side of Kuhn's story, his attempt to argue that individual narrowmindedness is all for the best in science. Back in chapter 5, I said that it is often hard to distinguish the descriptive from the normative in Kuhns discussions. Feyerabend saw this ambiguity in Kuhns writing as a deliberate rhetorical device for insinuating into the reader a positive picture of the most mundane type of science. For Feyerabend, the mind-set that Kuhn encouraged also leads to a lack of concern for the moral consequences of scientific work.
Feyerabend also argued that Kuhn was factually wrong about the role of normal science in history. According to Feyerabend, paradigms almost never succeed in exerting the kind of control Kuhn described. There are always imaginative individuals trying out new ideas.
Feyerabend was not, as he is sometimes portrayed, an "enemy of science." He was an enemy of some kinds of science. In the seventeenth century, according to Feyerabend, science was the friend of freedom and creativity and was heroically opposed to the stultifying grip of the Catholic church. He admired the scientific adventurers of this period, especially Galileo. But the science of Galileo is not the science of today. Science, for Feyerabend, has gone from being an ally of freedom to being an enemy. Scientists are turning into "human ants," entirely unable to think outside of their training (1975, 188). And the dominance of science in society threatens to turn man into a "miserable, unfriendly, self-righteous mechanism without charm or humour" (17 5). In the closing pages of Against Method, he declares that society now has to be freed from the strangling hold of a domineering scientific establishment, just as it once had to be freed from the grip of the One True Religion.
7.5 An Argument from History That Haunts Philosophy
Let us now look at the argument that is perhaps most central to Feyerabend's work. This is an argument from history.
A large part of Against Method is taken up with a discussion of Galileo's arguments against his Aristotelian opponents in the early seventeenth century (see section z.5). Galileo aimed to defend the literal truth of Copernicus's claim that the earth goes round the sun rather than vice versa. One of the things Galileo had to confront was a set of obvious arguments from experience against a moving earth. For example, when a ball is dropped from a tower, it lands at the foot of the tower even though, on Copernicus's view, the tower has moved a significant distance (along a huge circle) while the ball is in the air. All of our everyday experience of motion suggests that the earth is stationary. These are not arguments from the wisdom of Aristotle or the sayings of the biblical apostles; they are arguments from what we observe every day. If empiricism in philosophy has any teeth at all, Feyerabend claims, it entails that people in the seventeenth century had excellent reasons to resist Galileo and believe that the earth is not moving.
Galileo, of course, rejected the arguments. In his Dialogue concerning the Two Chief World Systems ([16321 1967), he patiently tries to show that Copernicus's model is compatible with everyday experiences of motion. If the earth is moving, then a ball dropped from a tower has a mixed kind of motion. It is falling toward the earth but is also moving in a huge circle just as the tower is. Our everyday perception of motion is unable to distinguish the case where both tower and ball have a circular motion from the case where neither does.
Galileo defuses the argumen
ts, but he does not suggest that this is easy. Indeed, he marvels at Copernicus and others who have "through sheer force of intellect done such violence to their own senses as to prefer what reason told them over that which sensible experience plainly showed them to be the contrary" (quoted in Feyerabend 1975, zoz).
According to Feyerabend, what Galileo had to do was to create a different kind of observational description of the world, one in which descriptions of apparent motion were compatible with the Copernican hypothesis. Only then would the arguments for Copernicanism become plausible. What science had to do, here and in other cases, was to break through the constraints of an outdated worldview that had permeated even the most basic observational description. Science, for Feyerabend, is often a matter of challenging rather than following the lessons of observation.
What we see here is a simple case of something that Feyerabend regards as ubiquitous. A very basic empiricist principle, of the kind dear to philosophers, would seem to be pointing people in the seventeenth century away from the scientific theory that we think now to be true. The philosopher complacently spouts generalities about how science is great because it is responsive to observational data. But history suggests that the principles the philosopher likes so much would steer us in the wrong direction if people back in the crucial period had applied them.
Through all the exaggerations, deliberate provocations, jokes, insults, and outrageous statements in Feyerabend's works, this form of argument runs as a constant and challenging thread. Are there any principles of method, measures of confirmation, or summaries of the scientific strategy that do not fail the great test of the early seventeenth century? Look at the massiveness of the rethinking that Galileo urged, and the great weight of ordinary experience telling against him. Given these, would all traditional philosophical accounts of how science works, especially empiricist accounts, have instructed us to stick with the Aristotelians rather than take a bet on Galileo? This is the Feyerabendian argument that haunts philosophy of science.
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