Research Strategies

I thought we might begin to answer Matt DeStefano's plea for more autobiographical posts by discussing our research practices and strategies. If my own academic life is any indication (though it may well not be), it can take a very long time to develop effective strategies. My research processes today, for example, are far different than those I had as a grad student. Accordingly, I guess I'll share what they used to be compared to what they are now. Before I begin, I guess I should probably preface my remarks that follow with a couple of caveats. First, I don't pretend to believe that what "works for me" will work for everyone. We're all quite different. There are many ways to do things. Be that as it may, I hope that some of my experiences will resonate with many people. Second, I should probably be clear that I am not a publishing "rock star." While I've published work I'm proud of, I haven't published in tip-top journals. So, if you're a person whose highest aim is to be that sort of person (the person that I'm not -- at least not yet!), perhaps my example is not the best one to follow. All that being said...

As a graduate student, I used to spend months and months reading "everything under the sun", and then months and months on papers. This is quite natural in grad school, for obvious reasons. You're on a semester system, you have lots of free time, etc. So, you really have time to read a lot and then sit in front of your computer mucking around on a paper for months on end. Finally, it's not obviously irrational to do all of this, particularly when you can get feedback from fellow faculty members on your ideas and paper drafts. One important thing I learned in grad school is that it's super important not to do work "in secret." It's natural for some people (those of us who are somewhat insecure) to retreat away from advisors and fellow students, for fear that they'll think our papers are garbage. In my experience, the more that people shrink away from publicly discussing their work in grad school, the more trouble they tend to have finishing. This is in large part because other people will help you see flaws in your ideas much more quickly than you will on your own. I had this experience myself. I had been toying with an idea for six months and then when I finally presented a paper on it in a working-paper-group, it was clear to me that the idea was hopeless. If only I had gotten the idea out in front of other people sooner, I would have saved myself a lot of time. It's not easy to have others -- particularly your fellow students -- slaughter your ideas, but it is (I think) a necessary component to doing good research. More on this shortly.

I found, once I got out of grad school and into my first job (a VAP position), that I had to dramatically change my approach. Once you're out in the "real world", it's much harder to get feedback from your colleagues. First, if you're in a big department (which I was at the time), your colleagues likely have grad students they're supervising, so they likely have little time to read and comment on your work. Second, if you're in a small department (like I am in now), you just don't have colleagues to comment on your work. You can try having email exchanges with friends in which you comment on one another's papers, by for my part I haven't found this works very well.

Because of this problem, I found it necessary to fundamentally change my approach to research. My first year out, I researched like I did as a grad student: spending months reading and the months writing. But nothing panned out. It was hard to "vet" my ideas, because I just didn't have people to read paper drafts and such. So, here's what I did instead.

I started my publishing career by publishing two "replies" (see here and here). I think replies are a great way to get one's career started for a number of reasons. First, they just don't take long to put together. Scan the literature -- particularly top journals -- for articles you find interesting. Read them relatively quickly. If anything pops out at you as clearly mistaken, write up a 2,000 word paper that very briefly gives background to the paper and then, as clearly and quickly as possible, drives a strong objection home. Then just send them out. Don't waste time getting them vetted by colleagues. Just get them out to the journal and move onto the next (note: don't just send out terrible pieces of junk; you should only send out a reply if you feel pretty confident the piece is strong). Do several of them. You might get some rejections, but chances are, you'll get an acceptance or two and you're published. Just like that.

The second thing I found useful about replies is that they helped me change my entire approach to research. Replies, as I've just indicated, can be put together quickly (in a matter of days). In my own case, this helped me to become more efficient. Once you're out in the "real world" as a faculty member, you have far less time to screw around (teaching takes up a lot of time, at least if you want to do it well). Further, as I noted above, you have far fewer opportunities to "vet" your ideas with others. You just don't have mentors around like you did in graduate school. And so it's not a good idea (in least in my experience) to spend months and months farting around on papers. Instead, I've adopted something like Linus Pauling's famous claim that, "The best way to have a great idea is to have a lot of ideas." Here's what I often do. I read something, I have an idea about it, I write it up in 3,000 words in a matter of days, I send it to a conference, and leave it at that. If it gets accepted at conferences and I get good feedback, I work on it more, developing it into a full-fledged paper to publish. If it gets rejected everywhere, I tend to figure, "Well, that idea didn't work out -- let's move on." In short, I try to write lots of short papers quickly, get them out to conferences where I can "vet" them and get feedback, and then go from there. Ever since I started doing this, I've been more productive (writing lots of papers), enjoyed research more, and published more, than I did before.

I guess I'll finish this post by briefly discussing two strategies I have for coming up with papers. The first strategy -- which, for some reason seems to work very well for a lot of other people but not for me! -- is what I like to call the "workmanship" approach. Here, the process is similar to the one I discussed above for replies. You read some papers in top journals, find some problems with what you read, and write a very targeted, rigorous paper that motivates an objection to the going views you've read and motivate some positive thesis. If the top-journals are any indication, this seems to be how most people who are successful proceed. Most of the paper's I've read in top journals recently seem to have something like this structure: "In recent articles on X, authors A, B, and C have given argument P for Q; I'm going to show that P fails, etc."

I frankly haven't been too successful at this approach, though I continue to work at it. Because of my struggles at being this type of philosopher, I began experimenting with another approach: one that comes far more naturally to me by temperament -- what I like to call the "paradigm busting" approach. Here, my approach is not to scour the literature looking at particular arguments people have given, but instead to survey the literature on a topic to see how people across an entire discipline or sub-discipline look at a particular problem. Oftentimes, what I find is that I sort of think everyone is looking at the problem in a rather unhelpful way. So, instead of engaging with particular arguments that other people have given, I simply give a positive argument of my own for thinking that the arguments themselves are beside the point (as founded in an incorrect paradigm). So, for example, in this paper I argue that human rights have been misconceived; in this paper I defend a theory of free will that I believe "squares the circle" between libertarianism and determinism; in this paper I argue that we shouldn't be so concerned with how Kant understood the Categorical Imperative but rather with how it can be understood -- in light of Kant's overall project -- to unify the various formulas; etc.

This is, I think, a different way to go about writing papers. I don't "pore" over the literature when I adopt this approach (as opposed to workmanship approach, which I also pursue). Instead, I try to work out problems from the ground up (viz. "What exactly do I think Kant is trying to do in his practical philosophy? How do I think the literature on Kant doesn't match up with how I think his project should go?").

Now, I suspect there are some out there who will "diss" this approach. And indeed, I haven't published in top places. Maybe the approach won't pan out. Who knows? I guess I'd rather "go down swinging", doing stuff I truly believe in, and which I think represents who I am as a person and a philosopher.

Comments

[Lisa]

Thanks for this post, Marcus! I totally sympathize with choosing the second over the first approach. In my experience, such papers are harder to get into good journals. My tentative explanation is that the review process is biased in favour of what you call the "workmanship" approach - it's "safer", you can get more "rigorous", and it's clear for the editors who can review your paper (and unless you completely destroy their arguments, they will feel flattered that someone takes their work seriously and thus are likely to recommend publication). But paradigm busting is SO MUCH MORE FUN!!!! For writers and for readers! I sometimes fear that all this workmanship stuff takes the soul out of philosophy, really… I hope many people read your post and do a bit more paradigm busting!

[Matt DeStefano]

Marcus, thank you! This is incredibly helpful. I am very much in the same camp as you were in graduate school with regard to how I write papers and how I do my research. Similarly, I also find myself rather hesitant to share my work with others, but this post definitely will help motivate me to do so more often. The advice on reading journals and writing replies is very helpful, and exactly what I was hoping to get with my plea.

[Marcus Arvan]

Thanks Lisa! And I'm glad you found it helpful, Matt. I plan for this post to be the first in a series. So thanks for issuing your plea!

[Roman]

There is also the possibility of doing a hybrid of workmanship and paradigm busting: do the workmanship on a particular philosopher's work, but situate it as paradigmatic. That combines the simplicity of the former approach with the excitement of the latter, although granted that it risks not being as exciting for readers who haven't read the particular person you are engaging with.

[Marcus Arvan]

Roman: No doubt. I've tried to go that route in my work on Rawls. I've found, though, that it's perhaps the most difficult way to go of all. When a particular figure (like Rawls) has already been written about so much, I think there are at least two additional possible sources of resistance to paradigm busting: (A) professional "fatigue" about the theorist (viz. resistance to publishing yet another article on the figure), and (B) people who specialize on the figure having their "mind made up" in advance on how the figure should be understood.

An example: I actually had a well-known reviewer leave his name in the "properties" section of the PDF I received with his journal review, and advocate rejecting the paper on the basis of the fact that his considered view about Rawls (which he has published extensively on) is the opposite of mine. Something similar has happened to me a few different times.

Anyway, none of this is to say that paradigm busting can't be done (or done well) on particular figures. But I do think it's perhaps the hardest sort of project to be successful at. Sometimes I rue the day I was ever introduced to Mr. Rawls. ;)

[Roman]

Marcus, that's a good point. One way I tend to approach this is to write on a relatively new figure who has not been written about extensively, but who has a somewhat paradigmatic defense of a particular position. Of course you still have the problem of reviewers who agree with the paradigmatic position and recommend rejection on those grounds, but that's going to be a possibility with any kind of peer review as long as you are making any controversial claims.