How to develop new research projects?

In our newest "how can we help you?" thread, a reader asks:

I'm an early career academic (in my first job post PhD). I've recently finished a couple of drafts based on PhD chapters and sent them to journals, and now I don't really know what to do next! This is the first time since my PhD began where I have had to effectively start from scratch. I'd love to know how academics navigate this - when faced with a blank page, how do you decide what to start working on next? What criteria do you use? My job is only temporary, so there is also the pressure of producing enough publications to make me a good candidate for jobs in a few years time.

These are great questions that, in my experience, many early-career people have. Indeed, I struggled with them earlier in my career myself! One reader submitted the following reply:

I have been a relatively successful researcher - for whatever that is worth. I would recommend that you extend your research into a neighboring topic, that is, investigate something near to what your thesis was on. Alternatively, go deeper into a topic that you have written on in your dissertation. You need to build on your strengths, and get some publications under your belt. And the best way to place them in good journals is to develop depth and build on your strengths. 

This seems like good advice, but I think there are other options too. In the past, I've shared some of the ways that I've found work for me in terms of developing new projects. For example, in this post, I shared the following three suggestions:

1. Anytime you have any idea for a potential project, jot it down in a notebook. Keep a running list of ideas, and then do some background reading in each area to see whether the idea has any promise (given what has been written in the area).
2. Keep an eye out for CFPs on PhilEvents, particularly ones that only call for abstracts. I had a few projects develop this way, as getting an abstract accepted gave me an excuse to work the paper in question up.
3. Just read widely in new areas: this is something I was advised to do by a mentor in grad school when I was struggling to come up with a dissertation topic. I had previously been spending most of my time reading one area of literature (moral responsibility and motivation), and I wasn't able to come up with anything good. Then, after my mentor told me to read around, I started reading in political philosophy--and I came up with my dissertation idea in just a few months!

Similarly, in this post, I shared how most of my published work emerged from the following:

1. Teaching
2. 'Going back to basics', or the foundations of a major philosophical problem
3. Isolating and questioning an assumption that nearly everyone in a literature seems to accept
4. Reading widely, including well outside of philosophy and in the history of philosophy and science
5. Having a major project that has long-term development potential

Indeed, I can't overemphasize just how many of my research projects came from exploring ideas while teaching, both new material as well as canonical works. Teaching, in my experience--especially with undergrads--requires one to develop a clear commonsensical understanding of even the most difficult works, and to think about all of the different ways one can question the works and surrounding philosophical debates in question. 

Finally, in contrast to the reader who initially responded to the OP--who suggested working in neighboring areas to the OP's previous projects (which seems like fairly good general advice)--my own approach to developing new research projects is quite different. I remember reading somewhere a while back Linus Pauling's saying that "the best way to have a good idea is to have a lot of ideas." This is basically my approach. I mostly pursue whatever philosophical ideas occur to me, regardless of how closely related they are to my previous work, work them up into paper drafts, submit them to conferences, and so on. I call this the "throw everything at the wall and see what sticks" approach. It may not work for everyone. But I've found it an exciting and enjoyable way to approach research, and it's enabled me to publish fairly widely. I'll also note, since the OP mentioned they are only in a temporary position and need to publish a lot, that I adopted this approach back before I had a TT job, and found it enabled me to publish more (I think) than I would have had I focused my research more narrowly.

But these are just my thoughts and experiences. What are yours? "When faced with a blank page, how do you decide what to start working on next? What criteria do you use?"

Comments

[FC]

I've started to look at ways my project and work area generally are treated in a non-Western intellectual tradition. It's been very interesting.

[Jay]

Read the abstracts of new papers. When you find an interesting paper, read it. If you disagree with it write a paper explaining why the author is wrong. If you can't find a way to disagree with the author, move to the next interesting paper.