Alex Guerrero (Rutgers) on research methods

Over at Daily Nous last week, Alex Guerrero (Rutgers) shared some really helpful advice for applying to PhD programs. But, in addition to being helpful for grad applicants, I actually think his remarks on writing samples may be helpful for graduate students and other early-career scholars who are struggling to publish. Here are the key passages that I have in mind:

Let me begin by saying some possibly controversial things about how good philosophy comes into existence. I’ll begin by describing a method that rarely works. First, start with an interest in some topic that has been discussed a lot by philosophers. Second, read everything on that topic, over a long time, keeping kind of neutral notes on the views throughout. Third, try to think of something new to say. Disaster!

Maybe some people can do it that way, but it’s very hard to find your voice and keep your passion and energy throughout that process. Instead, you learn about the 18 moves that have been made, the 14 positions in logical space that have been occupied (like tanks running over flowers), and you can maybe spot another 2 or 3 that haven’t been occupied. You can write a paper that takes up one of those, but often you aren’t really excited about that position, it’s just kind of left over. And maybe for a reason…

Much better: start with something that is bugging you or disturbing you. Maybe it’s an actual thing in the world that is happening. Maybe it’s an idea that was presented in a class that just seems wrong somehow. Maybe it’s some text or topic that seems philosophically interesting, but which no one is talking about. Maybe it’s just a way of looking at things that comes to you from who knows where, while your mind wanders around (like flowers growing over tanks).

What I find so interesting about this is that the first method--the method that Guerrero says rarely works--is the one that I initially adopted when trying (mostly in vain) to come up with a viable PhD dissertation topic. After my comprehensive exams, I spent something like one-and-a-half years doing just that: reading everything on moral motivation, taking copious notes, and trying to come up with something new. It was a disaster. I found myself in exactly the position Guerrero describes: I knew the "14 positions in logical space" that everyone had already occupied, as well as the 2 or 3 that hadn't because, well, those positions were obviously wrong. So, I couldn't come up with anything! It was like running into a brick wall, day after day after day. Then, I did what Guerrero says to do instead. I found something that was bugging me. I read Rawls again, and noted that he never did nonideal theory in any kind of systematic way, and that no Rawlsians really had either. So, I immediately had an idea--to use Rawls's machinery to develop a nonideal theory of justice--and wrote a dissertation on it. Just like that!

Anyway, it's really amazing what a simple change in research methods like this can do, so I figured that I would not only share it--as I expect there are probably grad students and early-career philosophers who are struggling to come up with dissertation ideas and publishable work. I also figured it might be good to see (1) whether other readers have found Guerrero's approach to research beneficial, and (2) whether you have any research tips of your own! Any readers care to weigh in what you've found helpful in coming up with good research ideas or otherwise being productive as a researcher?

Comments

[Robert A Gressis]

From 2005-2016, I wrote on Kant, in particular, Kant's theory of evil and his philosophy of religion. My motivation for writing on Kant's theory of evil was not that I found it particularly interesting, but rather that my best grade on a paper in one of my first graduate classes was on Kant's theory of evil. I figured if I did well on that paper, I must be good at that topic, so I wrote on that topic.

That was my motivation. As for my approach, I would read lots and lots of Kant -- like, all of Kant -- and take notes on anything that I thought might be relevant to his theory of evil. My note-taking approach was to simply write, word for word, what Kant wrote (or was said to have lectured about) and then color-code it in my notes, depending on what I thought it was about (e.g., if the phrase was about why we act immorally, I would put it in red font; if it was about why the human race is or isn't naturally evil, I would put it in blue font, etc.).

Besides reading Kant, I would also read a lot of the secondary literature, and any time someone said that Kant said so-and-so at such-and-such place, I would look it up and see whether I agreed with what the writer thought Kant was saying. If I didn't, I would take note of *that* and build up a database of a way to respond to critics.

This was extremely laborious, and it wasn't fun, and it was a great way to read instead of write. I did this up until 2016, at which point I decided to write about the epistemology of disagreement, because that whole topic had been bothering me and make me question why I even was a philosopher for about five years, if not more. For that area, I taught a class on the epistemology of disagreement. I still did a lot of reading, but what was different was that it was a lot more emotionally involving than my Kant reading. I really cared about the outcome of each paper! It was also a lot easier to remember what each paper was saying and to figure out how to respond to it. I eventually published a paper as a result of that experience.

Finally, I started writing for the public philosophy website, The Electric Agora. Here, I would simply think about something, write about it, and then get comments from the community there. I would rarely read secondary literature. It turns out, this approach was the best for writing. And it was actually quite easy to use this approach to write scholarly papers. Here was my approach:

1. Find something that was bugging me.
2. Write about it.
3. After I wrote about it, I would read the secondary literature.
4. Because I already had a view, and because the view had been formulated without reference to the literature, I would often find that I had a different take on things. It was then really easy to have something new to say.
5. Rinse and repeat.

[postduck]

I think this advice from Guerrero could really go either way, and that it might actually not be the best advice for people applying to PhD programs. We all like to complain about boring philosophy papers that just add one more incremental move to some existing, overwrought debate. This is in large part because that's what most published philosophy papers are like; if you're not working on the specific debate in question, chances are these papers will be super boring to you. And so when we're writing our own dissertations and books and papers, we strive to break free of this mold when we can. Fair enough.
But then I think about the kinds of papers that most undergrads and MA students write, and I think, "Gee, if they could really chart out an entire complex debate and find an original position within it, that would be a real accomplishment." I actually do see a lot of undergrad papers following Guerrero's advice and writing things that just seem interesting to them, and they're usually terrible! A lot of students write philosophy papers with grandiose delusions that hinge on a combination of ignorance and confusion. And that's not their fault: doing original work is really hard, and you need to get pretty good at planning and writing papers and thinking through philosophical problems to do it well. It's probably the sort of thing most of us don't really get good at until we've spent a good deal of time in grad school. I see the first, "boring" kind of paper as an important stepping stone to that, and a real accomplishment in its own right. I'm not on an admissions committee or anything, but I would think that an undergrad or MA student who can display that sort of competence is probably good grad school material.
Granted, there probably are a some PhD applicants out there who actually can write genuinely original philosophy. But I'm willing to bet it's a very small fraction of the people who would make perfectly good philosophers. Maybe it happens because they had great mentorship, or because they got lucky and happened to have the right combination of ideas. Or maybe it's because they're "natural talents" or "geniuses" - though I am inclined to think that that's actually a very distorted way of thinking about philosophical abilities, and that it's a real problem for our discipline that we think this way.
But of course, programs like Rutgers are not interested in students who would make perfectly good philosophers - they're looking for the cream of the crop. Maybe they're even looking for geniuses or natural talents, I don't know. But evidently they do look for papers that are genuinely original and have they special "je ne sais quoi." It doesn't really matter for them that it's unrealistic to expect most undergrad or MA students to write this way - even straight-A students with top GRE scores. They can afford to be picky.
But does this mean it's good advice to tell prospective graduate students (most of whom *won't* get into Rutgers) "don't bother writing papers that just competently lay out a debate and carve out a novel position in it"? I doubt it. I am willing to bet that for many students applying to Rutgers, trying to write the way Guerrero suggests would be miserable and counterproductive.
To my mind, writing "boring" philosophy papers still a pretty valuable skill that we shouldn't turn up our noses at just because our field has a problematic culture of brilliance.

[postduck]

PS: I know this post was how Guerrero's advice might be pretty good for early career folks and grad students, and I think I agree with that (especially for early career folks). I'm mostly just reacting to the way the advice was originally aimed, which was as a thing you should do when applying to grad school.

[Overseas Tenured]

One type of paper that I began writing in great numbers over the past few years is a paper that tries to clear up my own confusion. I’d often read on a topic and gradually realize that there is something basic I don’t understand. I chat with people, and often conclude as a result that the thing in question is genuinely unclear, in a way that people deeply involved in the debate missed. So I write up a whole paper on how this or that notion or thesis, central to a debate, is totally unclear. I was able to publish many papers of this form on top journals; I also found it much more fun to write them than narrow interventions.