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03/15/2013

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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... ;)

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