Should early career philosophers devote time and energy to writing journal articles on figures, topics, or debates that are moribund, marginal, or otherwise unlikely to gain interest among other philosophers? Obviously, this turns on complicated metaphilosophical and professional issues too large for a blog post, so let me offer an autobiographical perspective, following Thi Nguyen’s approach in an earlier post in this series.
I did my doctorate at Durham University, starting in September 2006, submitting exactly four years later. My topic was the neglected later writings of the still-controversial philosopher of science and self-styled ‘epistemological anarchist’, Paul Feyerabend (1924-1994), author of Against Method. In terms of publishing articles on his later work, the prospects were mixed. On the one hand, Feyerabend was considered old hat. Genuinely important in his day, sure, but relative to ‘old-school’ concerns, no longer on the agenda of philosophy of science.
On the other hand, the later Feyerabend offered possibilities for publication. First, the paucity of interest meant there was a scholarly space to fill – an attractive prospect for an early career scholar. Second, there was material in his later writings useful to contemporary, ‘hot topic’ debates in the philosophy of science – pluralism, say, or the epistemic authority of science in democratic societies. Given this situation, a professionally smart thing to do would’ve been to write articles on Feyerabend’s arguments for pluralism in science, keying into work emerging from North American philosophy of science. Such articles could (a) draw on my doctoral work and (b) resonate with active and emerging debates in philosophy of science, including (c) the ‘live issues’ that the ‘top’ philosophy of science journals would likely find attractive.
I did not do these smart things.
Instead, my first two published articles on Feyerabend treated themes so esoteric I doubt even the specialist Feyerabend scholars read them. ‘Objectivity, abstraction, and the individual’ appeared in Studies in History and Philosophy of Science in 2011. It explores an unusual influence on Feyerabend’s epistemology – the 19thcentury Danish philosopher Søren Kierkegaard, melancholy author of such existentially brooding works as Fear and Trembling. Struck by Feyerabend’s effusive praise of him, and intrigued as to the nature of the influence, I followed up his references to Concluding Unscientific Postscript, eventually working out how Kierkegaard’s critique of the abstraction and systematicity of Hegel’s philosophy had informed Feyerabend’s philosophical methodology. The second article, ‘Feyerabend, Pseudo-Dionysius, and the Ineffability of Reality’, began with my being struck by Feyerabend’s claim that his later metaphysics was inspired by De Divinis Nominibus, a mystical treatise byPseudo-Dionysius the Areopagite, a 4thcentury CE Christian Neoplatonist. Careful reading shows that his conception of the ‘divine names’ really had informedthe later Feyerabend’s ‘ineffabilism’, as developed in his final, unfinished book, Conquest of Abundance.
As much as I judge these papers genuinely worthwhile for intellectual and scholarly reasons, deciding to write them – rather than ones on pluralism, say – could, in some respects, be regarded as a bad idea:
- Feyerabend was not regarded as ‘hot’, ‘trendy’, or otherwise attractive to the ‘top’ philosophy of science journals (or, in the UK, the ‘REFable’ journals).
- The specific topics were unconventional, isolated from mainstream debates, and pretty esoteric even relative to Feyerabend scholarship.
- The articles didn’t key into active, mainstream debates.
- The articles were unlikely to be of interest from any of the relevant scholarly communities (Kierkegaard scholars aren’t really interested in the philosophy of science and the Dane isn’t of any interest to either philosophers of science or Feyerabend scholars).
- The comparative methodology is one that some philosophers find dubious (surely one could, in principle and with ingenuity, take anytwo philosophers, however historically and intellectually distant, and find somethingto riff on for six thousand words?)
- A pair of articles exploring connections between existentialism and mystical theology and philosophy of science are likely to perplex (even alarm) a search committee considering me for a Lectureship in Philosophy of Science.
I was aware of all of this, of course, and my supervisor was consistently excellent in balancing encouragement of my intellectual autonomy with wise professional guidance. I recall, though, my main reasons for deciding to write those papers:
- I wanted to better understand features of Feyerabend’s philosophical work that seemed intrinsically interesting and intellectually valuable for their own sake.
- I was fascinated by Feyerabend’s eclecticism and enjoyed seeing the breadth and openness of his imagination – for instance, of how Kierkegaard’s critique of Hegel fed into the epistemology sketched in Against Method.
- I enjoy comparative work – taking seemingly disparate topics or traditions and seeing how they relate to one another, which is even more fun when one knows in advance that xinfluenced y.
- I enjoy working on neglected topics and underexplored areas, especially when it seems no-one else would be sufficiently interested or disposed to explore them.
- I thought that if my career was going to be short-lived, then I really ought to write the papers I wantedto write, not those that professional prudence dictated that I should.
Of course, there were ‘bad’ reasons, too. I’m bad at self-discipline, being typically unwilling to tame my intellectual enthusiasms even in the face of good countervailing professional reasons. Moreover, I’m prone to an epistemically egoistic sense of pleasure in being the only personto have acquired esoteric expertise on such obscure topics.
Gathering all of this together, let me end with these thoughts:
- The journal articles that best reflect your fascinations, enthusiasms, and sense of intellectual autonomy might not be the journal articles most likely to do any real professional work for you.
- The decisions you make about which journal articles to write are structured by a complex set of considerations – eg the fluctuations of trends, the different tastes of different journals and editors, the respecting rankings of different journals (the ones that might take your paper might not be among the ‘top’ journals).
- You need to be aware of your own epistemic and professional psychology – eg your ability to recognise and play into emerging trends, your willingness to do so in ways that honour your sense of intellectual integrity, the extent to which you could be content with writing the papers that matter to you when these may not be those that reliably advance your professional interests, the likelihood of your feeling bitterness or sadness if you elect not to write that one paper dear to your heart.
- You need to bear in mind your capacity for writing and the personal and practical resources available for it. If you can write a lot, then publishing on moribund or marginal topics is less professionally risky, which is my approach. But if you know you can write just one paper a year, maybe don’t devote it to an esoteric topic – do work that will do work for you.
- Seek guidance and advice from your supervisors, colleagues, peers, mentors. But beware that people differ – a lot – in their attitudes towards journals, their views on the relative weightings of intellectual ideals and academic realities, and their approaches to professional advancement. (I was once advised to pick whatever topic happened to be ‘hot’ in philosophy of science and write on that, regardless of whether it reflected my interests – an attitude I still regard with anathema).
- It’s important to be aware of whether one’s interests are likely to be regarded as esoteric. Granted, opinions differ, for all sorts of good and bad metaphilosophical and ideological reasons. But awareness of the sorts of responses one’s topics are likely to elicit is crucial for deciding how to pursue and present one’s research to others – at conferences, on a webpage, in job talks.Indeed, being able to track what’s ‘trendy’ is an important academic skill, regardless of whether you plan to play into trends or not.
The question of whether early career philosophers should devote energy to writing articles on marginal, neglected topics turns on particular and personal considerations. It also depends the character of your own scholarly self-conception – of your relationship to your intellectual interests as they will play out relative to the current tastes and trends of academic philosophy. Unfortunately, not all intellectually worthwhile projects are likely to do real professional work for you in the sense of getting you published in the sorts of ‘job-getting’ journals. That doesn’t mean one’s prospects are thwarted – far from it! It’s just that exploring the neglected areas is often lonely work that means one’s professional journey may tend to be longer and harder.
Ian James Kidd
University of Nottingham
Many thanks to Helen de Cruz, Havi Carel, Katherine Furman, Thi Nguyen, and Tom Rossetter for their helpful comments and encouragement.
These days, "don't publish on topics you're really interested in until you have tenure" basically translates to "don't publish on topics you're really interested in." I mean, some people have no real interests and will simply chase the market, and some people happen to have interests that align perfectly with market preferences. For everyone else: publish what you want, because otherwise you'll probably never get to.
Posted by: Roman Altshuler | 03/04/2019 at 06:33 PM
Hi Ian: Thanks for another great post!
For what it's worth, I'd caution early-career people against being too concerned with (1) ("The journal articles that best reflect your fascinations, enthusiasms, and sense of intellectual autonomy might not be the journal articles most likely to do any real professional work for you").
Following Thi's recent post, I think the bigger problem may be a tendency of early-career people to write on things that *don't* reflect their fascinations--because they think they need to write on "hot topics" in order to publish.
My experience cohered with Thi's. It was that not writing on stuff that truly fascinates you is a #1 way to kill one's joy in doing research. It was only once I started actually writing papers on stuff that fascinated me that I began to have any success publishing--and, more importantly, actually enjoyed writing and doing research.
Anyway, you note this yourself in (3) ("You need to be aware of your own epistemic and professional psychology..."), so I guess my message to early-career people would be: when (1) and (3) conflict, consider going with you actually find fascinating. It may be the only way to enjoy your work, and who knows? You might just do great work in the area because you love it--and other people might find it fascinating too.
Posted by: Marcus Arvan | 03/04/2019 at 07:00 PM
Marcus: quite so! One can say to the determined trend-chaser: you either follow your own interests, or you're following someone else's, thereby placing yourself in a situation of willed submissiveness and giving that someone a disproportionate power they don't necessarily deserve. This might relate to another rule: "invite but don't demand interest in your own work."
Posted by: Ian James Kidd | 03/04/2019 at 07:14 PM
If anything, I wish I had written more on topics I really care about. For me, that is a bit of a problem, because the topics I really care about are not the type of papers typically published in top journals. There are exceptions, of course, where a top journal publishes something from a small, interdisciplinary area of philosophy. But if you look at Mind and PPR there won't be a lot of these papers. I also wanted an R1 job. However I have managed to do well with publishing in top speciality journals, and doing a couple of more main stream pieces to show I have the skills to do that type of work. The problem is, if I am not doing work I love, I do less of it and do it less well. One of thing that really matters, I think, to both R1 and other universities is that you are a major player in your field. I think if you don't like your research this is unlikely to happen. And who wants to do research they don't like, anyway? So, while, I think there are some exceptions to this rule, it is generally a good idea to do what you like. An exception might be that if the area you like has almost no jobs, then you might want to consider a second best option. I.e. if you do philosophy of math AND really care about getting a TT job maybe you can see if there is another area you care about.
Posted by: Amanda | 03/05/2019 at 08:35 AM