Query on developing research projects post-PhD

A reader wrote in by email:

I'm not long out of graduate school, and now I've got to get some publications under my belt. I'm okay with diligence, but now that I'm not working on the dissertation and don't have a committee steering me with a moderately heavy hand, I'm having a heck of a time finding rich research projects and identifying good potential essays to work on. I've got a handful of smaller ideas (here's a minor objection, here's a quibble something buried deep in that literature), but nothing that seems remotely like the sort of idea that'd become a great article. Do other people have that problem? Do people have good strategies for getting on track?

I looked at Karen Kelsky's Unstuck program, but that seems more like it is for people who have a project but just can't quite bring it to the submission stage. Does anyone have experience with this program or some other coaching program that they wouldn't mind sharing?

This is a really great query. I struggled with the same issue my first couple of years post-PhD. While I had projects from my dissertation to work on (which is a good source for potential publications), I hardly got anywhere with coming up with substantial new projects. I read a lot and tried to write a lot...but the only ideas I came up with for a year or two were the kinds of 'minor' objections or quibbles this reader describes--stuff that seemed philosophically banal and nothing like a major research project? Fortunately, I learned a lot from the experience--both about what didn't work (for me, at least), but also methods for coming up with major new projects (something I no longer struggle with). While I don’t have any experience with coaching programs, let me describe my experiences and tips, and then invite you to share yours!

My first year or two post-PhD, I did what seemed to me the natural thing for coming up with new projects: I buried myself in the recently published literature. I read papers published the past several years, tried to find ones that I thought were interesting or mistaken, and then tried to come up with new paper topics on broadly those grounds. While this seemed like the natural thing to do, I found it didn't work for me for a number of reasons. First, it didn't feel very original or creative (the things about philosophy that I find most exciting). I was sort of just futzing around with other people's ideas--which, while it may be able to result in publications, wasn't all that fun. Second, it mostly led to 'small', piecemeal projects--that is, single papers rather than anything like a long-term, fruitful research program.

So, burying myself in the literature didn't work. What did? In my experience, it's natural to think that in order to be productive as a researcher, one should try to protect as much of one's research time as possible--by, for instance, teaching classes on stuff you know really well and can "teach in your sleep." This is exactly what I did my first two years out. It didn't work at all--and my experience has been that, for me at least, this is entire strategy is precisely wrong. Almost all of my major research ideas have either come directly from teaching or from experience in the world outside of reading books and journal articles. Allow me to explain how and why.

Teaching new courses: Teaching new courses has been one of my biggest sources of new research ideas. For instance, I never really did research on human rights before coming to my current institution. Then I got here and elected to teach an upper-division seminar on them. After reading and teaching several books and a bunch of articles in the course, I came up with a long-term research idea: that the human rights literature was generally based on a mistake, which I subsequently aimed to begin to rectify and have some further ideas to develop moving forward. The thing about teaching new material--especially upper-division seminars--is that it really requires you to survey, think through, and discuss with others a really wide-ranging set of issues. This can be helpful in coming up with big, long-term research ideas (rather than quibbling interventions) in that it encourages you to "see the forest for the trees"--not getting hung up on this article or that article, but on how people in a given literature think in general. If you think you find a flaw in the literature as a whole, you have a major research project: a negative project of showing how the literature is messed up, and a positive project of rectifying the flaws you believe there to be.

Going back to basics (in teaching!): Teaching has been a major source of research projects for me in another way, this time in introductory-level courses. I've heard really successful and influential researchers say before "don't read too much." I didn't used to know what they meant by this, but now I think I do. Reading too much--getting lost in the literature--can lead you down the garden path toward "thinking the way that everyone else thinks" about a given problem. The contours of a vast literature can (quite inadvertently) constrain your thinking, preventing you from "thinking outside of the box." Teaching introductory-level courses--and more than that, teaching material you think you know well going "back to the basics"--can in my experience be very helpful in coming up with new ways to think about things. Here are two examples from my case.

Case #1: Prior to coming to my current institution, I didn't work in ethical theory or Kantian ethics. I had a good background in these things (they were areas I did comprehensive exams in during grad school), but I didn't actively do research in either area. Then I taught an intro-level course here, and made it my aim to teach Kant in a way that makes intuitive sense to first-year students rather than getting lost in Kant's technical concepts or line-by-line readings of the text. While this was a real challenge (for obvious reasons), I've long believed the maxim, "If you can't explain it simply, you don't understand it." So, I tried to reconstruct Kant's thinking in my own head--my intuitive gloss on what he "was up to"--explaining that simple, intuitive gloss to my students, and only then turning to the text. This process--of simply trying to make Kant clear to my students in down-to-earth terms--turned into this paper, where I move from a simple intuitive picture to a textual interpretation that unifies Kant's different formulas.  That paper in turn led to my book, which in its initial draft defended a reconceived form of Kantian constitutivism (before I decided that was all wrong and rewrote a very different book!). All this from just trying to make Kant clear to first-year students!

Case #2: I've long taught my intro to philosophy courses as surveys (spanning philosophy of religion, metaphysics, epistemology, ethics, and political philosophy). While I've been rethinking this lately, it has been a real source of long-term research ideas--specifically, my work on free will and a new version of the simulation hypothesis. I always taught the basics of the free will problem in my intro class: the consequence argument, compatibilism, incompatibilism, libertarianism, etc. But I was sort of bored by it, and so it seemed were my students--who didn't seem at all interested in some of the standard issues in the area (Frankfurt cases, etc.). Because in my intro courses we went over Descartes' Meditations, the nature of reality, and arguments for mind-body dualism before discussing free will, I started just playing around in class discussion with other possible ways we might think about free will. Since the simulation hypothesis seemed to me possibly help us make sense of why a bunch of things--causation, personal identity, mind, and free will all seem to be "further facts"--and how, like, PacMan's "free will" is caused by his "user" in a higher-frame of reference, I decided to actually start thinking about these things more seriously! And, since I read a lot of physics in my spare time--and I knew a lot about problems with existing interpretations of quantum mechanics (and the fact that we don't have any deep explanation of why our world is quantum mechanical)--the stuff I was reading in physics led me down a new rabbit-hole: the idea that the simulation hypothesis can also help us understand fundamental physics and a variety of philosophical problems. All this from messing around trying to make an intro class more interesting!

Reading outside of philosophy: At any given point in time, there are (as I think we all know) fads and conventional ways of thinking in philosophy. It's easy once again to get one's own thinking hemmed in by the ways other people are thinking. Reading outside of philosophy can in my experience encourage a new perspective on things. For instance, I mentioned my book was initially a reconceiving of Kantian ethics. I then rewrote the book from the ground up. Why? Because of the history of science and behavioral neuroscience I was reading. Reading the history of science got me to question dominant methods in moral philosophy--methods I was using myself in the first version of my book. That led me to defend different methods-methods I argue ultimately require basing normative moral philosophy on empirical moral psychology and a naturalist reduction of normative moral semantics. Finally, the stuff I was reading in empirical psychology led me to the view that morality is very different than standard moral theories hold. The book has received mixed reviews so far, but whatever: it's led to an even longer-term research program of further defending, elaborating, and (yes) revising the theory in ways that have been fun and fruitful.

Getting your head out of books and articles, and live a little: Finally, I want to underscore something that Recent grad wrote here, that all too often new and interesting philosophical ideas--and research programs--can come not from burying your head in books but instead by living. As I mentioned here, my research program on free will and simulations emerged out of playing videogames and recording music! By a similar token, in addition to reading philosophy of science and empirical psychology, a lot of the ideas in my book came from life experiences, experiences in my marriage, watching and thinking about films and television episodes, experience with political polarization in politics, following the news (viz. international conflicts). So, I'd suggest, if you're having trouble coming up with ideas, get out and live, and reflect on your life and the world around you outside of books and journal articles: you never know where your next philosophical insight will come from!

Of course, these are just things I've found helpful. What about you? Have you encountered the problem our reader wrote in about (coming up with new research programs post-PhD)? If so, do you have any tips of your own for overcoming it? I'm really curious to hear people's tips and experiences!

Comments

[Michel]

+1 to Marcus's advice.

Getting a research *program* going is a bit different from getting research done and published, since it requires you to identify bigger-picture themes or concerns. Sometimes you can get there pretty quickly just by thinking about what topic you'd like to give a book-length treatment, and why. But I think a lot of the time, it's something we only really start to identify once we've already got a lot individual pieces out there, and someone or something prompts us to think about how they all fit together. It's hard to come up with a research agenda a priori; it's a lot easier a posteriori.

On the general publishing front, I'd say that your first quick source of pubs is your dissertation. The research is already done, and has been peer-reviewed a few times. The only thing left to do is to break it up into article-appropriate chunks. That can take some time, especially if you didn't write it with that in mind, but it's still faster than writing something new from scratch.

As far as writing from scratch goes, I'd suggest:

(1) Keeping a document/notebook/whatever where you keep track of paper ideas as they come to you. Just blurb the idea, make a note of what prompted it, and note any extant research that comes to mind which you should consult or cite. When you're out of ideas, have a look at that list and see what speaks to you.

(2) Start by writing those small, technical, quibbly replies. At 3k-4k words, they're appropriate for Analysis and Thought, and other journals which publish short pieces. But also, crucially, they're conference-length (not to mention a friendly length for peer comments). So now you can shop them around a bit, and see if others can't help you expand them into a more substantial article. Plus, once you've got something like that nailed down, it's easier to see if you can work it up into something broader. So, for example, maybe your dissent over X is actually inspired by a broader disagreement over the constraints on a practice P, the intelligibility of some background assumptions, etc.

I don't set out to write papers that are 7.5k words long. I set out to write a solid 3k-ish paper, and then think about what more there might be to say. Sometimes it's obvious, and sometimes I only get there after having shopped the paper around a bit and hearing what others have to say on the subject. The downside is that this strategy can take a little while to bear fruit, and once it does, you tend to have a bundle of stuff coming out all at once. The advantage, however, is that you've got something to show at each step in the process (besides which, it's much more pleasant to build a conference paper than it is to cut up an article so that it fits the time slot). And conferencing helps to build up a file of paper ideas, too. If you're cutting up your dissertation, then that will buy you some time to work up from shorter papers.

[Michel]

I forgot to add that if you're really stuck for paper ideas, you can draw inspiration from conference and special issue CFPs.

[Recent grad]

To add on to your comments on teaching:

I've started spending two meetings on readings I used to spend just one on. It's been great on a number of fronts, including increasing student comprehension and willingness to do the reading. But it allows helps me think about the material in ways I feel I can often turn into a paper. For example, I now sometimes teach the Experience Machine over two days and we look very closely and very critically at the three reasons he gives not to plug in (whether they're good reasons, whether they all reduce to the first, whether there are other potential reasons, etc.). There's a lot there.

[ash]

I agree with Michel that publishing research and developing a new research program are distinct things.

For most people (there are exceptions), the dissertation sets one's research *program* for several years. Hopefully it is also the source of some publications; you work a couple of chapters or portions of chapters into stand-alone articles. But even after you've done that it typically continues to set your research program, insofar as you're developing papers on ideas related to the dissertation. (Sometimes these are ideas one had to set aside in writing the dissertation in order to make it more focused; often you're continuing to read and to debate the issues after the defense, and you get more ideas there; etc.)

Developing a second research program (which often doesn't happen until near or after tenure) is a separate issue. For most people it seems to develop organically in some (possibly only tangential) way out of one's first research program. But "organically" means in part "slowly" here. I'm not sure how to do it quickly, though Marcus's advice all sounds good to me.

[The OP reader]

Thanks all! Much appreciated! I will take this advice into account--both the specifics and the encouragement it provides. I will definitely look for opportunities to add variety to my teaching that can open up potential new areas for work, and I really like the idea of slowing down working through the material. In future semesters, I think I will try to switch around between ordinary pace readings and slower readings so the students see both versions--and so that I maybe get some new ideas! And I'm gonna keep the conference-and-smaller paper work going. Get a bunch of those bubbling, and just keep faith that they'll build.

Thanks again! (And I'll keep watching around here for other ideas. The more strategies the better!)

[Paul]

I think this is good advice in general, its always a good idea to "write what you teach and teach what you write" insofar as is possible. I also really like the idea of reading outside of philosophy, and while you're at it, why not incorporate some of that reading into your courses? My upper division electives the last few years have been about 60% philosophy and 40% psychology. This is not only really fun and useful for me, but I think it also makes philosophy appealing to a much wider range of students. (I think this can be done in an intro course as well, but probably not to that extent). And with more and more interdisciplinary philosophy journals out there, this can provide good fodder for research.