More Derumsfeldifying the Profession

I came across Dan Dennett's brilliant little essay "Higher-Order Truths of Chmess" again today (which I've quoted large sections of below), and it occurred to me that the essay arguably falls under the embella of De-Rumsfeldifying the Profession -- the task of figuring out "what we didn't know we didn't know" about our profession (see here for an initial foray).

It's clear, when looking at both recent and long-term history of philosophy, that our profession is quite faddish. Some things -- some topics, some arguments, some philosophers -- are all the rage for a few years or decades, and then are mostly forgotten about. Robert Filmer, for instance, was apparently a "very important" political theorist...that is, until John Locke eviscerated his defense of the divine right of kings in the First Treatise of Government (an evisceration so thorough that no one bothers to read it anymore). Or what about ordinary-language philosophy? All the rage in analytic philosophy...until people recognized it for what it is: hair-splitting. 

None of us, I hope, want to do philosophy that is merely faddish. We want to do philosophy that is truly important. But how? How do we determine what's important and what's not? Obviously, we can't just look to our peers -- because it's the very point of fads that everyone thinks they're awesome...until everyone realizes they're not.  So, how does one tell? 

For my part, I find Dennett's proposal pretty compelling.  According to Dennett, if you can't make the point of what you are doing -- the issue/argument that you are concerned with, etc. -- intuitively clear to a smart undergraduate, the issue/argument is probably BS. I have this experience with a surprising number of well-known philosophical arguments and figures in the classroom -- and so I think it's a great test. If we can't make the importance of a problem or argument clear to the uninitiated, then maybe, just maybe, we're caught in a fad.

Which brings me, finally, to another thing I think some of us "don't know we don't know" -- namely, how very important teaching (I'd say, specifically undergraduate teaching) is to research. I recall reading somewhere that the famed physicist Richard Feynmann refused to give up his undergraduate teaching duties because of how teaching undergraduates forces one to make issues clearer and more intuitive than in other contexts (in sharp contrast, Einstein, as soon as he stopped teaching, stopped doing the intuitive physics that made him famous and got lost in abstract math that never led to much of anything).  

Yes, experts and grad students "know what you're talking about" (or at think they do!) when you get into really technical stuff -- but it's also easy for people deeply in the grip of a problem or dialectic to "lose touch" with other important things: namely, making sure that the "problems" they are dealing with are really problems. Indeed, one problem with graduate students is that, however more sophisticated they tend to be than undergraduates, they (grad students) have been philosophically domesticated. They're "in the game" in such a way that they (sometimes) uncritically accept the existence of problems, and the "importance" of arguments/figures, simply because "those are the important figures/arguments" in grad school/the profession. Undergraduates, however, are comparatively blank slates. Teaching them effectively requires you, as a philosopher (or physicist, or whatever), to make the problems you are concerned with clear and intuitive. Anyway, this is how I find it. Most of the "good ideas" I think I've had have emerged from just trying to make things clear and intuitive for undergraduates.

Anyway, I've been at this post for too long now, so I'm just going to leave it at that and open it up for discussion. Oh, and without further ado, some of Dennett's remarks:

Some philosophical research projects-or problematics, to speak with the more literary types-are rather like working out the truths of chess. A set of mutually agreed upon rules are presupposed-and seldom discussed-and the implications of those rules are worked out, articulated, debated, refined. So far, so good. But some philosophical research projects are more like working out the truths of chmess. Chmess is just like chess except that the king can move two squares in any direction, not one. I just invented it-though no doubt others have explored it in depth to see if it is worth playing. Probably it isn't. It probably has other names. I didn't bother investigating these questions because although they have true answers, they just aren't worth my time and energy to discover. Or so I think. There are just as many a priori truths of chmess as there are of chess (an infinity), and they are just as hard to discover. And that means that if people actually did get involved in investigating the truths of chmess, they would make mistakes, which would need to be corrected, and this opens up a whole new field of a priori investigation, the higher order truths of chmess, such as the following:

1. Jones's (1989) proof that p is a truth of chmess is flawed: he overlooks the following possibility...

2. Smith's (2002) claim that Jones's (1989) proof is flawed presupposes the truth of Brown's lemma (1975), which has recently been challenged by Garfinkle (2002). . . .

Now none of this is child's play. In fact, one might be able to demonstrate considerable brilliance in the group activity of working out the higher order truths of chmess. Here is where Donald Hebb's dictum comes in handy: "If it isn't worth doing, it isn't worth doing well."

Each of us can readily think of an ongoing controversy in philosophy whose participants would be out of work if Hebb's dictum were ruthlessly applied, but we no doubt disagree on just which cottage industries should be shut down. Probably there is no investigation in our capacious discipline that is not believed by some school of thought to be wasted effort, brilliance squandered on taking in each other's laundry. Voting would not yield results worth heeding, and dictatorship would be even worse, so let a thousand flowers bloom, I say. But just remember: if you let a thousand flowers bloom, count on 995 of them to wilt. The alert I want to offer you is just this: try to avoid committing your precious formative years to a research agenda with a short shelf life. Philosophical fads quickly go extinct and there may be some truth to the rule of thumb: the hotter the topic, the sooner it will burn out.

One good test to make sure you're not just exploring the higher order truths of chmess is to see if people aside from philosophers actually play the game. Can anybody outside of academic philosophy be made to care whether you're right about whether Jones's counterexample works against Smith's principle? Another good test is to try to teach the stuff to uninitiated undergraduates. If they don't "get it," you really should consider the hypothesis that you're following a self-supporting community of experts into an artifactual trap.

Here is one way the trap works. Philosophy is to some extent an unnatural act, and the more intelligent you are, the more qualms and reservations you are likely to have about whether you get it, whether you're "doing it right," whether you have any talent for this discipline and even on whether the discipline is worth entering in the first place. So bright student Jones is appropriately insecure about going into philosophy. Intrigued by Professor Brown's discussion, Jones takes a stab at it, writing a paper on hot topic H that is given an "A" by Professor Brown. "You've got real talent, Jones," says Brown, and Jones has just discovered something that might make suitable life work. Jones begins to invest in learning the rules of this particular game, and playing it ferociously with the other young aspirants. "Hey, we're good at this!" they say, egging each other on. Doubts about the enabling assumptions of the enterprise tend to be muffled or squelched "for the sake of argument". Publications follow.

So don't count on the validation of your fellow graduate students or your favorite professors to settle the issue. They all have a vested interest in keeping the enterprise going. It's what they know how to do; it's what they are good at...And here the trap to avoid is simply this: you see that somebody eminent has asserted something untenable or dubious in print; Professor Goofmaker's clever but flawed piece is a sitting duck, just the right target for an eye-catching debut publication. Go for it. You weigh in, along with a dozen others, and now you must watch your step, because by the time you've all cited each other and responded to the responses, you're a budding expert on How to Deal with How to Deal with Responses to Goofmaker's overstatement. Neither the truths nor the falsehoods of chmess are worth a career.

Of course some people are quite content to find a congenial group of smart people with whom to share "the fun of discovery, the pleasures of cooperation, and the satisfaction of reaching agreement." as John Austin once put it, without worrying about whether the joint task is worth doing...Austin was a brilliant philosopher, but most of the very promising philosophers who orbited around him...have vanished without a trace, their oh-so-clever work in ordinary language philosophy duly published and then utterly and deservedly ignored within a few years of publication. It has happened many times.

So what should you do? The tests I have mentioned-seeing if folks outside philosophy, or bright undergraduates, can be made to care-are only warning signs, not definitive. Certainly there have been, and will be, forbiddingly abstruse and difficult topics of philosophical investigation well worth pursuing, in spite of the fact that the uninitiated remain unimpressed. I certainly don't want to discourage explorations that defy the ambient presumptions about what is interesting and important. On the contrary, the best bold strokes in the field will almost always be met by stony incredulity or ridicule at first, and these should not deter you. My point is just that you should not settle complacently into a seat on the bandwagon just because you have found some brilliant fellow travelers who find your work on the issue as unignorable as you find theirs. You may all be taking each other for a ride.

Comments

[Moti Mizrahi]

Hi Marcus,

I'm not sure that "making things clear and intuitive for undergrads" is a good test of "philosophical importance." But I think you are right about how teaching undergrads can be an effective way to generate ideas for one's own research. In fact, I just posted on the Cocoon a paper of mine that emerged from teaching logic and critical thinking at the undergraduate level.

[Marcus Arvan]

Hi Moti: I agree it's not the only test, but I still think it's a helpful one. It's hard to know if something is a fad "from the inside." Getting outside the discipline -- trying to justify the importance of problems to smart people who haven't "drank the cool-aid" already -- is one way to go about doing it. It may not be the only way, or even the best way, but it is one way. Do you think there is a better test?

[Lisa]

Hi Marcus,
talking to smart people who are not even interested in philosophy as such - i.e. not philosophy undergraduates, but "normal" people with jobs, families, kids, political views, etc. - is another thing you can do.
One might say: that tests for social/political/whatever relevance, not philosophical relevance. But then at least for some areas of philosophy, the former kind of relevance should also, to some degree, inform the latter (e.g. what is a just society? how should we deal with stem cell research? what is the meaning of life, love, religion, etc.). So depending on what one is interested in, this can also be a useful strategy for finding out what might be good research topics. You can then use the history of philosophy and all the systematic arguments that have been made in this area (or indeed other areas - sometimes analogies can work as well) of philosophy and work out what they mean for this particular question.

[anonymish]

I don't know about a fool-proof test. Smart undergrads can be taken in by a philosophical scam, just as smart philosophers can.

How's this for a test: articulate to *yourself* why topic or problem X is interesting. This is my test, and it's tangentially relevant to earlier discussions about blind refereeing. Trust in thyself, and lean not on the status of another to legitimize thy judgments or interests. Follow this rule, and you don't need to google people's papers as much. Nor need you worry as much about whether your project is misguided.

Caveats exist, I know. But if I can convince myself that a project is interesting or a paper good, that's enough for me (for present purposes). At least I know where I stand w/r/t that thing.

[Walter]

This may be of interest. James Ladyman recently published "Philosophy that's not for the masses" (The Philosopher's Magazine, 2011, Issue 53, 2nd Quarter). I'm not sure Ladyman completely disagrees with Dennett, but he does take up the other side of the issue, i.e., he argues that it is not important for philosophers to able to explain a lot of what they do to non-experts.

http://tinyurl.com/bh7ypes

http://reallyducksoup.blogspot.com/2011/05/philosophy-thats-not-for-masses.html

[T.M.]

It looks like Ladyman argues it is not important for all philosopher to actually explain what they do, or to make their work always accessible in lay terms.

Anyway, I am sure one would want to distinguish between (1) being able to motivate your research project's importance in general, by connecting it to issues outside of the problem area itself, (2) being able to explain technical questions and issues in less than one undergraduate class, or 2 hours, etc..

Just think of how mathematicians and scientists explain their work and its importance as a research program. If you are studying wasp mating patterns, body segmentation patterns fruitfly development, or ordinary or technical concepts of causation, it is easy to say why anyone would care about any solutions to any problems in the vicinity. Maybe some research programs have no worthwhile payoffs, and this seems to be Dennet's point. Alfred Kinsey began his career studying wasp sexuality, and decided it was more worthwhile to study human sexuality, presumably for this reason. It is one thing to describe something's philosophical importance by referring to extant literature, another thing to describe its importance simpliciter.

[Marcus Arvan]

Lisa: I entirely agree. As "anonymish" points out, undergraduates can be scammed into "drinking the cool-aid" too. Maybe the best test is to try to motivate problems to "wider audiences" of smart people in general -- friends, colleagues in other disciplines, etc.?

Anonymish: I grant your point about undergrads, but I'm skeptical about the "justifying to yourself" as a test, as it's easy to justify something to yourself once you've already downed the Kool-Aid (so to speak!). Isn't this how "scholastic" philosophy gets rolling to begin with (a bunch of people who are so deeply in the grip of a theory or worldview that it's just "obviously" justifiable from their point-of-view)?

TM: nice points -- though I think there are lots of reasons not to think "worthwhile payoffs" is a good test. The history of mathematics and science is full of discoveries that resulted from inquiries that seemed to lack *any* possible real-world payoff at the time.

[T.M.]

I know that, and I agree, Marcus. Just two things to add:

First, because of the track record of basic science and pure math, there is some reason to pursue such work. However, I am not entirely confident in whether that model holds today. It was much more plausible in the 1950s when things like work on the atom, etc., had enormous impacts, people were constantly drawing on centuries old math, and much was still open. There may be such diminishing returns that pure basic research is far less justifiable today than even half a century ago.

Or rather: you can do both at once: http://en.wikipedia.org/wiki/Pasteur's_quadrant

Second, and more to the point: the decision to be made is what to spend one's time doing. A choice between two options. When one has a clear potential payoff and the other lacks one, go with the more promising research program. If there is no clear payoff, aside from within-the-tradition stuff that Dennett talks about, the choice is between continuing the present research program or looking for its payoffs (or other programs), so the same reasoning applies.

[Marcus Arvan]

Hi again TM: I guess I still demur on both points. First, I'm not sure there are the diminishing returns that you speak of, or that things were much more wide open in the 1950s. People have long supposed that "things used to be wide open, but not so anymore." It was said in Newton's time that physics was all but over...until it wasn't. Then, of course, it's *now* suggested that we're almost there, what with the success of relativity, QM, the Standard Model, etc. -- this despite the fact that (A) all of these areas of physics are estimated to only deal with 10% of the observable universe, (B) we don't have any adequate quantum theory of gravity, and (C) the other 90% of the universe is supposedly made of dark matter and dark energy, neither of which we have a good understanding. Who's to say the same kind of pure (read: "useless") research that led to current physics won't lead to breakthroughs once again (given, especially, the history of things working out that way)?

Here's one recent example: twistor theory in mathematics. As I understand it, people doing twistor stuff were regarded as cranks fiddling around with useless formalisms. Well, until Ed Witten demonstrated that twistors can be used to embed 10-dimensional string theory in a 3-dimensional space-time. Further, twistors may also turn out to be helpful with quantum gravity. And that's just one case!

Anyway, it's for roughly these reasons I also resist your second point. I wouldn't want to choose something that appears to have "clear payoffs" over something that doesn't, in large part because what appears to have payoffs at any given time seems in large part determined by how people conventionally think about things at that time -- and I think most important breakthroughs occur by flouting convention.

But anyway, back to philosophy... ;)