The following opinion piece is one of a series of five being released this week and next to celebrate World Philosophy Day and to publicise the upcoming workshop entitled Editor’s Cut – A view of philosophical research from journal editors. the workshop will take place at the University of London on Friday 13th of January 2012.
What caused the demise of logical positivism? According to certain potted histories of 20th-Century philosophy, it was Willard V.O. Quine’s refutation of central claims about analyticity in “Two Dogmas of Empiricism” that did it, or Thomas Kuhn’s refutation of logical positivism’s claims about science in The Structure of Scientific Revolutions, or it was problems about how to understand the verification principle (is it itself verifiable?) that did it in. These explanations are problematic. Quine just didn’t give any compelling argument against analyticity in “Two Dogmas of Empiricism”. At best he argued that it couldn’t be non-circularly characterized, but the same goes for many perfectly legitimate notions, and notions Quine accepted as perfectly legitimate – as H. P. Grice and Peter Strawson were quick to point out. As for Kuhn, it has now been well-documented that Rudolf Carnap, the most famous logical positivist, was quite positive about Kuhn’s project. Simplifying somewhat: while Kuhn presented an account of actual history of science, the positivists discussed science under a certain idealization. Kuhn does not even talk much about logical positivism in Structure. Problems regarding the verification principle are another matter. Those problems are arguably serious. But they weren’t discovered when logical positivism met its demise. (Which was when, exactly? The 1950s? Early 60s?) Rather, such problems were alwayswith logical positivism, having been pointed out by its earliest critics.
Instead, something like the following happened. Logical positivism presented a certain kind of research program. Its tenets presented certain questions as the ones research should be focused on. But gradually the suggested research program came to be seen as somewhat sterile. It became natural for theorists to look elsewhere. Insofar as Quine and Kuhn had important roles to play it was rather here. Kuhn’s work suggested a research program rather more focused on the actual historical development of science. And while the early parts of Quine’s “Two Dogmas” present a rather unconvincing argument against the notion of analyticity, the latter parts present an alternative, holistic picture of theories – and this positive picture, while not argued for, can have been seen as a fruitful alternative to the then sterile-seeming picture presented by the logical positivists. (A complication is that Carnap had presented a not too dissimilar picture already in the 1930s. But Carnap didn’t highlight the picture in the way Quine did.)
I think this tells us something about how philosophy often develops. Without borrowing wholesale Kuhn’s picture of science, I think some ideas Kuhn introduced are important to keep in mind when considering the trajectory of philosophy. Research programs are adopted, consciously or not, by a certain part of the philosophical community: certain tenets are taken for granted, certain notions are regarded as the proper ones to use as tools, and certain puzzles are regarded as the ones to focus attention on. The research program isn’t abandoned simply on the ground that seemingly compelling arguments against its fundamental assumptions are presented. Rather, it is abandoned when research conducted within its confines is no longer seen as fruitful, and when a new alternative, with some promise of success, is available.
Some recent developments seem to fit this template well. (1) Experimental philosophy (“x-phi”). The emergence of x-phi, with its emphasis on empirical, statistical methods in philosophy, isn’t due to some particular novel arguments on its behalf, or against the ‘armchair philosophy’ it sets itself up against. Rather, certain early results seemed exciting and suggestive of more exciting results to be had. New avenues of research opened up in areas that seemed stagnant. (2) Within contemporary metaphysics it has become popular to focus on fundamentality, essence and grounding, and on thinking about ontological questions not as questions about what there is but about what there is, fundamentally. There are, to be sure, arguments supporting use of these notions: arguments to the effect that modal notions don’t suffice to draw all distinctions we may want to draw. But the point about the insufficiency of the modal notions is relatively obvious, and the recent surge of interest in these more fine-grained notions can’t really be the result of some new insight. Better to look at things as follows: It has been known for some time that modal notions cannot be used to draw all distinctions that can intuitively be drawn; it was just that a time came when it seemed to many more fruitful to look at what can be said about fundamentality, grounding, etc. than to stick with the old framework and try to use only modal notions for serious theorizing.
I think further examples can easily be provided. But every example one might be tempted to give will be somewhat controversial, for friends of the philosophical approach in question will be tempted to say that the development is more argument-driven than I give it credit for, and sometimes such a reply will be correct.
One sometimes hears the complaint that contemporary philosophy is too trend-driven. I am sure I have sometimes snarky remarks to that effect myself. The above considerations can be seen as reinforcing such complaints. One can take what I say in the previous paragraph to suggest that the developments I consider there are mere fads. But while there may be reason to be skeptical of some of the developments that fit the general template I describe, that’s not what I take the main lesson to be. Instead, I think that it is inevitable that the kind of thing I describe often happens. And while this may not immediately constitute progress, a means to progress is to keep looking for where there is interesting research to be done and progress to be made. Some research programs popular at a given time can perhaps be dismissed as mere fads, but it is easier confidently to make such assessments given proper hindsight.