Saturday, June 15, 2013

Jottings on Philosophical Problems

When it comes to philosophy, two difficult things to teach (and also to avoid falling out of practice with) are the following two principles:

(1) Problems are not automatically transparent.
(2) Not all problems are fatal problems.

The first is particularly difficult to teach, and is something that even professional philosophers can become lazy about. It is not sufficient to pose something as a problem for a position; what everyone needs to know is why it is a problem and what kind of problem it is. Many supposed problems turn out to be nothing more than misunderstandings based on differences in vocabulary. We see this a lot, I think, with counterexamples. Merely proposing something as a counterexample to a claim does not mean that you have actually proposed a counterexample. Your supposed counterexample may end up being nothing of the sort. Alternatively (and this happens quite often), one might have something that is only a counterexample with additional assumptions that may be controvertible. (Of course, it's also possible that it turns out to be an even better counterexample than we originally thought; this doesn't happen often, but it does happen.)

Putting something forward as a problem for a position is therefore the beginning of a new inquiry; a first step, not a final one. The problem needs to be articulated with at least a reasonable degree of precision and accuracy. Depending on the circumstances this can be quite complicated. One of the things historians of philosophy do is articulate (or re-articulate) problems in a certain context, compare them to each other, see how they've influenced each other, and so forth; it is what keeps us in business. It's also what keeps us arguing with each other. This is where most people trip up when it comes to (1). Suppose we are talking about the mind/body problem. We cannot in fact assume that there is only one mind/body problem; it may be, but we have to establish that. It could be that there are lots of very different mind/body problems, depending on certain background assumptions; it could be that there are possible assumptions that involve no mind/body problem at all.

We must also identify the way in which it is a problem. Some problems are structural problems: there is at least some reason to think that the problem is inconsistent with the position at hand. Some are discovery problems, by which I mean that there is at least some reason to think that something a position requires cannot be found, or that something will be found that a position requires not to be there. For instance, if someone proposes the evolution of the eye as a problem for a theory of evolution, this would involve proposing it as a discovery problem: this particular theory should be able to find (somewhere along the line) an adequate evolutionary account of the eye but we have some kind of reason for thinking that it won't succeed. Another way to look at this distinction is that completely fatal discovery problems are established inabilities to accomplish something, usually a search for something, while completely fatal structural problems are established contradictions. Yet another way we can present the distinction is as one between static and dynamic features of the argument or position; arguments and positions do not generally spring full-grown from the skull like Athena, but are constantly in the process of being constructed. If we think of arguments, positions, theories, etc., as a building that is going up, structural problems are weaknesses in what is built, discovery problems are obstacles to building it. The two may be connected, so that a structural problem uncovers a discovery problem and vice versa; I think, in fact, that people often implicitly have the goal of finding interconnected networks of structural problems and discovery problems, because structural problems can sometimes be patched and discovery problems sometimes evaded or worked around, but doing both simultaneously generally requires rethinking everything that is proposed from the ground up. But it's important to note that even if one thing were both a structural problem and a discovery problem, its being the one is distinct from being the other, and the kinds of responses that are reasonable will often differ depending on which aspect you are considering.

To make clear whether a problem is a structural problem or a discovery problem is another thing that requires that the problem be carefully articulated. For instance, the interaction problem is often put forward as a structural problem for Cartesian dualism, but it is in reality a discovery problem, being about something that Cartesian dualism doesn't seem to give us much hope of understanding very well; it is often confused with Princess Elisabeth's determination problem, which in fact does seem to be a structural problem, depending directly as it does on basic principles of Descartes's entire account.

This distinction between structural and dynamic problems should not be confused with that between what I will call research problems and fatal problems. Suppose you've articulated a problem. What then? One mistake that has to be avoided is assuming that identifying a genuine problem is the same as developing a refutation. Problems are not refutations, although fatal problems are the basis of refutations.

Most problems are not fatal; they just indicate points where construction of a theory, position, or argument is unfinished. These are research problems: they show us that at present such-and-such is unsolved, and not an actual inability to solve it. (This is why both structural problems and discovery problems can be research problems: it's not about whether the solution can be discovered but about whether it is actually in hand.) If we take something like a particular theory of evolution, this theory by its nature creates a massive numbers of problems. The overwhelming majority of these are research problems. Some of these research problems may be so complicated that it would take years to solve, and yet they could still be soluble. So if I were to take a particular case, like the evolution of the eye, and show that the theory could not at present handle it, I have to consider the real possibility that this is just because there's work to be done developing the ideas and principles of the theory, and not because the theory can't handle the case at all. Far from being refutations, research problems are often essential to the construction; just as architecture is the art of organizing material design solutions, so also building a theory is the art of organizing solutions to research problems.

In general, in fact, there are two kinds of research problems: inquiry-structuring research problems, which are the matter-of-course next steps that every theory or position naturally suggests to the human mind, and inquiry-baffling research problems, which are problems that pull us up short and force us to ask the question, "How in the world would one go about handling this?" There is no sharp line between these two. In any field the problems people are most interested in are both inquiry-structuring and inquiry-baffling -- they are the problems both that we need to use to develop our ideas and that we are not sure how to solve. These are the exciting problems, the ones that require breakthroughs.

One reason this is all important is that people often treat research problems as fatal problems, because, identifying a genuine problem, they think they are done, whereas their problem may not be fatal at all. A great many things that pass for refutations are not real refutations; they are just extremely difficult research problems, research problems in which people are getting bogged down, and proposed solutions keep failing. This is serious, certainly, but hardly refutation; there are lots of things that could be happening. It could be that a false assumption is being made that, when rejected, will open up the way to the solution. It could also be (and this happens very often in the history of philosophy) that people just lack the infrastructure to do the research properly. If a school is small, it may not have enough people working on any given problem to have more than very sporadic progress. Some problems require specific kinds of data, which may be difficult for people working on the problem to get. Some entirely soluble problems just require so much work given the resources at hand that the time required to solve them would be extraordinary. And so forth. These infrastructural pseudo-refutations are quite common: people claim that advocates of such-and-such position are unable to solve problem X, and then pass on, not stopping long enough to check whether any appearance of this might just be because they need more time, or because they don't have enough people of the right background working on it. That is, it may in reality have nothing to do with the position itself. The interaction problem for Cartesian dualism has all the marks of being a non-fatal research problem, for instance: there was never any positive reason to think that, given extensive enough research, Cartesians might not be able to give excellent answers to it, at least as excellent as anyone can give concerning any other kind of interaction. Likewise, it's one thing to pose a problem and give reasons why you think it can't be solved, but demanding that people develop a flawless solution to a new problem on the spot is irrational. Very baffling research problems are not the same as fatal discovery problems; we need additional positive reasons to think that a problem is the latter.

But, of course, even fatal problems are not the end of the road. Hume notes in one of his essays that one of the remarkable features of human thought is that we can build even on our errors in the pursuit of truth, and this is certainly right. A particular position or theory might have a fatal problem, something that it simply cannot solve with its own resources or any resources that could be consistently added to it, and still be valuable for inquiry. It might serve as a stepping stone to some better position, analogous but importantly different, that is not subject to the same problem. Indeed, coming to understand why the first position won't work may be the essential element in coming to understand why the second will. Thus the fact that a theory, position, or argument has a fatal problem does not mean that it should be despised as worthless; fatal problems too are only beginnings of further inquiry. Perhaps this should have been added as my third point above.

2 comments:

  1. skholiast1:31 PM

    Excellently put and salutary. As has been frequently noted by historians of both science and philosophy, basic positions are almost never refuted; they go out of style. The fact that no one in one's temporal (not to mention departmental) vicinity seems to take a position seriously is all too often enough to persuade us that it ought not to be. So we frequently don't even get to the fatal objection stage, because these objections are presumed to have been made by someone else long enough ago that we need not concern ourselves. (Cartesian dualism is a case in point, thought a few brave souls soldier on, like Peter Unger.)

    Which is not to say that, if we rise above this kind of non-thinking, we never encounter what turn out to be serious problems, whether structural or research, fatal or non-. Just that it's hard to know when they are really there and not a figment of the atmosphere.

    Dennett says somewhere or other (probably in multiple places) that philosophy is what we do when we don't know what the right questions are. I think this is way too glib a way of casting philosophy as ancillary to the sciences, but your way of taxonomizing problems seems to have something in common with it, in a more open-ended and non-reductionist way.

    Do you know Michel Meyer's book On Problematology?

    ReplyDelete
  2. branemrys3:40 PM

    I know I haven't read it; but looking at both the title and description it sounds vaguely familiar, so it's conceivable I've read some discussion of it.

    ReplyDelete

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