Opportunistic writing

One of the great things about being a professional academic is that you get to write about whatever you want. One of the hard things about being a professional academic is figuring out what to write about and what not to write about. I'm curious to know how others approach this issue, but I'll begin with my own account as a cautionary tale.

Things were easier for me in graduate school. Once I'd chosen a dissertation topic, the next few years seemed pretty well mapped out. I'd spend a few years writing my dissertation, after which I'd spend a few more spinning papers out of the major chapters and building a research program on those first few papers. At first, things went according to plan. The dissertation came along at a nice clip, and one of the early chapters was accepted by a journal before I'd defended the dissertation. The paper containing my "main ideas," however, has languished at one journal or another for the past three years. Because it's somewhat idiosyncratic and has received mixed responses, I'm not sure about building a research program on it until it's published. I've presented versions of that paper at conferences and have made some progress on it. However, I'm lucky enough to be on the tenure clock now, and so I can't afford to twiddle my thumbs while journal referees twiddle theirs.

Without the direction established by my dissertation, I've taken what I'll call an "opportunistic approach" to writing. I have quite varied philosophical interests, and I've been indulging them whenever an opportunity presents itself to write a potentially publishable piece about one of those interests (e.g., a conference CFP, an interesting paper comes out about which I have something to say, an invitation to contribute to a volume, etc.). I suppose my strategy has been to try to grab some low-hanging fruit while trying to publish my "primary" research.

In short, this strategy hasn't worked very well. I've produced a bunch of (mostly unpublished) papers on a bunch of different topics. Aside from one coherent research program that's emerged from an opportunistic interdisciplinary collaboration with a friend, most of these papers are mediocre at best. There are two or three that might pan out, but I wouldn't be that surprised if they don't. I think I'm just not deeply entrenched enough in the relevant literatures to execute these papers well. What's more, many of the papers are on topics around which I don't really want to build a research program. If I can get them published, they'll be "one off" pieces. So, I don't have much incentive to get deep enough into the relevant literature to make the paper work.

What strategies have worked for people in identifying publishable ideas and/or fruitful research programs? What strategies haven't been working?

Comments

[Marcus Arvan]

David,

I struggled with the same issue my first couple years out, and I've found in my own case that certain types of "opportunistic" writing work whereas others don't. My first two years out I focused on what appears to be the kind you are talking about: the "low-lying fruit" type -- the kind where you find some recent article(s) or argument(s) and latch onto it. I've found that this type of approach doesn't work for more or less the reasons you mention: (1) the work I did was mediocre at best (in part, I think, because of a natural lack of passion for low-lying fruit), (2) I couldn't get a good enough of a handle on the (usually) large body of literature surrounding the issue, and (3) the papers were usually "one-offs", not the sort of thing I could develop into a real research programme.

Let me now turn to the kind of opportunistic writing that *has* worked for me. In contrast to the "low-lying fruit" kind, let us call it Big Idea Writing. Here, instead of beginning with a particular article or argument to respond to, I have focused on issues that I think *everyone* gets wrong. Here are a few examples (apologies for plugging my own work, but I think they're good illustrations of what I mean):

(1) In my recently published article, "Reconceptualizing Human Rights", I argue that *everyone* has thought about human rights in the wrong way, because the concept of a "human right" is semantically defective and must be replaced by two non-defective concepts: domestic human rights (to be enforced within states) and international human rights (which are to be enforced internationally).

(2) In my forthcoming paper, "Unifying the Categorical Imperative" (of which I have a much longer version in preparation -- see my post on similar articles for questions about this), I argue that *everyone* has the Categorical Imperative wrong, and that when one begins with Kant's screwy conception of practical reason it is actually quite easy to see how all of the formulations of the CI are (as Kant wrote) literally identical (or "several statements of the very same law).

(3) In my paper, "A Better Theory of Vagueness", I use a thought experiment to argue that *everyone* is wrong about vagueness, and there is an elegant and intuitive theory that immediately pops out once we use the thought experiment to systematize and test as number of independently plausible points.

Okay, enough plugging. ;) I have no idea how many of my arguments are any good. Of course, *I* think they're good, but maybe they're crap. Who knows! Here, though, is what I *do* know. First, when you write on "big ideas" -- issues that you think most if not everyone has wrong -- it brings a certain passion and excitement to your work that is simply missing with "low-lying" fruit. You no longer feel like you are splitting hairs just to get pulications. Instead, you feel like you are writing on something original and of real value. I can't emphasize this enough. I spend my first two years out working on "low-lying fruit", and drove
myself half-crazy doing work that *I* thought was mediocre. This brings me to my second point, which is that "big ideas" have a tendency to beget much greater productivity than "low-lying fruit.". In the two years I worked on low-lying fruit, I finished only two papers or so (only one of which was published, as a reply). I worked myself to the bone on papers that went absolutely nowhere (I count at least
five papers that I spent a great deal of time on onlyto give up on). In contrast, during the past two years -- my "big idea" years -- I have written *fourteen* full-length papers and published four of them. They've literary come popping out of me one after another. Now again, who knows how many of them are any good? But here's what I know: *I* think they're good, and more importantly, I'm absolutely loving doing philosophy. That alone, I think, is reason enough to pursue the big idea route. Low-lying fruit are boring; big ideas are *invigorating*! Finally, here's a thought that has guided me, and which I think makes sense: since there's always a chance that you won't get tenure, wouldn't it be better to fail really "going for it" (with big ideas) than to fail going after low-lying fruit? For me, at any rate, the answer is obvious. Either way things go -- tenure or no -- I'd like to look back feeling like I'd had real integrity, writing on ideas that move and enrapture me, instead of low-lying fruit that dimmed my soul...

[Marcus Arvan]

Oh, almost forgot. The "big idea" approach (often) also saves one from having to immerse oneself in a given literature. After, if you think *everyone* is wrong about some issue, all you need to do is give an overview of the prevailing views (which you can often do quite easily, using the Stanford Encyclopedia and simple web searches). Indeed,, all one often had to do is real *abstracts* of recent articles, and then skim the articles, to see that everyone is working within the same paradigm, such that you don't have to drive yourself crazy fully digesting everything to make your case for *your* big idea (you can simply write, "Everyone from A to B to C, etc. approaches the problem *that* way -- and I'm going to show that we should be thinking about it *this* way"). This aspect of the "big idea" approach is, I think, one of the strongest marks in its favor. One can spend far less time reading everything and far more time thinking and getting it all out on paper!

[Mark Alfano]

Interesting question, David. I think I'm in a somewhat similar position to you. The "money chapter" of my dissertation was rejected by several fancy journals, while other stuff related to the dissertation and to my other interests (e.g. Nietzsche) got accepted. What seems to have worked in my case was to repackage the dissertation as a book (two chapters removed, three added) and send that off for publication. I don't know how representative my experience with book referees was, but I found that they were much more invested in seeing the good qualities in what they were reading than journal referees, who often seem to be searching any excuse whatsoever to reject a paper. So, if your key chapter still hasn't been published, you may want to consider the book route. Books are also pretty helpful for making a tenure case, from what I hear.

[Marcus Arvan]

Very interesting, Mark. I was under the (apparently mistaken) belief that book publishers won't be all that interested unless you've already made a name for yourself in the relevant area. Given that I've had my "money chapter" rejected by a bunch of fancy journals too, maybe this is something that I should think a bit more about. Would you perhaps consider writing a short post on how to effectively seek a book contract? I think that would be awesome, and that a lot of people here might benefit from your experience! No pressure though... ;)

[Mark Alfano]

I'll see what I can do... just moved all my belongings back to the east coast, so things are kind of crazy at the moment.

[Mark Alfano]

In the meantime, the best publishing advice I've found is from Thom Brooks (http://papers.ssrn.com/sol3/papers.cfm?abstract_id=1085245). He has a section on book publishing, in addition to all the other stuff.

[David Morrow]

Thanks for the tips, guys. Sadly, I don't think my dissertation is book material. Since taking the main chapter of my dissertation in a new direction last year, I've toyed with the idea of expanding that into a book, but that seems like a large investment of time for a highly uncertain reward.

[Jack Gladney]

One piece of advice that might be useful here: Write the paper people will reply to, not the paper that merely replies to somebody else.

Why do I say this? Well, journals want to publish "original research," of course, and it may be that the "low-hanging fruit" you mention looks too much like a discussion piece and not the sort of thing that will generate new research, citations, fame and fortune. That is pretty general suggestion, but there you have it. (Really, this is just another way to suggest some of what Marcus has said. I also agree with his thought that you need to write on topics that seem worthwhile by your own lights.)

In the end, it's probably not a bad idea for a graduate student to look for some low-hanging fruit just to learn the steps. The fact is that writing for journal submission takes skills and nerve you don't pick up by writing term papers. So you start somewhere. Write that reply to Prof. Goofmaker's paper. Some young philosophers will start with a epochal, debate-shaping argument, but that's not the most of us (ever). And so I want to suggest there is indeed some value in at least going after relatively easier contributions, early on.

Which low-hanging fruit should you go for? At the moment, I can't think of anything in general that seems helpful. Here is some obvious stuff, I suppose. If the journal that published Prof. Goofmaker's paper tends to invite and regularly accept discussions of papers that appear in that journal, that's a plus. (Analysis and Philosophical Studies come to mind if M&E fruit you're after.) If Prof. Goofmaker is relatively famous, there is another plus. If Prof. Goofmaker is an unknown philosopher, that's a negative. If Prof. Goofmaker's argument wasn't a central contribution anyway (and no one would blink even if the argument didn't fail hopelessly), that's a negative.

What else can be said here, about identifying the marks of a worthwhile opportunistic project?

Here is some useful publishing & writing advice from Peter Smith (former editor of Analysis):

http://www.logicmatters.net/students/getting-published/

http://www.logicmatters.net/students/writing-style/

[Marcus Arvan]

Jack: all good advice, I think -- and thanks for the links!

[David Morrow]

I like that way of putting it, Jack.

Perhaps my use of the term 'low-hanging fruit' was misleading, though. In general, the issue isn't that I've just been writing replies to other people. Most of the "opportunistic writing" I'm talking about is written with some particular venue in mind--usually a conference on a particular topic, a special issue, an edited volume, etc. (In fact, the one "reply" that I've written recently came about coincidentally while I was brainstorming ideas for a paper to submit to a particular conference.) The reason I think of these papers as low-hanging fruit is because I feel like it will be easier to "do something with them," even if that's initially just presenting them at a conference. I also feel like it's some indication that the paper is on a topic in which other people are interested. But the end result has been somewhat lackluster, as I've said.

So maybe the question is this: Suppose you found yourself without any more works in progress, and you were deciding what to write about next. How would you go about choosing a topic? Marcus's suggestion is to go for "big ideas" papers of the form 'Everyone else who discusses topic T thinks that p, but I think that q.' He reports that this has worked well for him. What other strategies are working (or not working) for people?