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!
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