On what to work on
Short-term decisions, long-term planning, and developing a sense of taste.
Our time is finite. For many, a natural question thus arises about how best to use (or “spend”) that time. A microcosm of this question emerges in the case of academic research, where researchers are typically privileged to have a fair degree of autonomy over what they work on. How should researchers prioritize among the possible projects that present themselves?1
This is, fundamentally, a good kind of challenge. It’s one I faced often in graduate school: I was surrounded by interesting and intelligent peers working on all sorts of questions I’d never thought of before, and each of those questions felt like a tantalizing alternative to whatever project I was currently stuck on. Further, my PhD advisor was (fortunately) more of a mentor than a manager, which meant that he never forced me to work on “his” projects, but rather, used his expertise to help sculpt my vague interests into something resembling a research direction; that, in turn, required me to think about what I was actually interested in doing.
One of the most useful things my advisor did for me was to consistently ask, when presented with a proposed project, why one would do that project—what would they learn? I learned that there’s a difference between figuring out how to do something (and whether it’s even possible) and deciding that you should do it.
Still, I never really considered the question in terms of longer arcs of time. I thought about which project to work on next but not which kinds of projects to work on over many years. I was forced to consider that latter question in recent years as I applied for faculty jobs and was asked to develop a research vision; it was hard for me, but I do think I learned something about myself and how to think about the relationship between my interests and the ways I move through time.
In this post, I’ll describe a few ways of thinking about this question:
Putting one foot in front of the other: figuring out your next project.
Finding an “important problem” to solve, and how to find it.
Developing a sense of taste.
Notably, (1) and (2) conceivably fall under the same conceptual frame—i.e., “spending” your time effectively—and differ primarily in their sense of time horizon. (3), in contrast, focuses less on characteristics of the work itself (e.g., whether it is impactful) and more on one’s relation to that work. These days, I’m increasingly drawn to (3), but I think each of these approaches has merit.
(1) One foot in front of the other
A reasonable starting point might be to think primarily in terms of your next project. In the most extreme case, this might involve thinking day to day: each day you do some work, and you think about what you should do the next day. At a slightly less granular level, perhaps you think in terms of roughly “paper-sized” projects: the set of activities that will ultimate constitute a contribution to the scientific literature.2
Truthfully, I think this is how many people actually operate, including myself—and I think that’s entirely fine. To some extent, we engage in a kind of hubris when we suppose that we can plan for anything more distant than a single “move” away. There’s a sense in which the wisest strategy is to surrender one’s sense of control over the long arc of your life and instead focus on the daily choices that make up that life.
Moreover, you can still endeavor to make these choices intelligently, using whatever decision framework you prefer. You can think, for instance, about whether this paper or that paper would be a more useful contribution to the field (i.e., its “impact”), how much effort would be involved (i.e., its “tractability”), and whether someone else is likely to do it anyway (i.e., its “neglectedness”). In short, you can ask: is it worth doing?
Of course, looking only a single move ahead has its drawbacks. It’s already very easy in academic research to get lost in the details and lose sight of what your broader goal; if you don’t even have a broader goal other than your current (or next) activity, the winds of fate can easily buffet you into a region of decision-space that’s hard to escape. Maybe that means chasing down an endless series of package installations (and subsequent version issues) without asking whether there’s an alternative approach; or maybe it means chasing down a chain of references for a topic you weren’t even that interested in.
Again, there’s nothing bad about this: it’s more or less how I do things, and it leaves the door open for serendipity. But as a researcher, one of the most useful skills you can develop is an ability to “toggle between levels”, so to speak—it’s crucial to immerse yourself in the details of an analysis, but it’s equally crucial to have a kind of internal meta-cognitive monitor that can check in on your activities every so often and ask whether this is, in fact, a valuable use of time.
(2) Finding “important problems”
If (1) looks one “move” head, then the aim of (2) is to look at your “destination” and figure out how to get there. What kinds of problems do you want to solve in your career?
The underlying assumptions here are that it is possible to reason at all about something with such a broad temporal horizon, and that it makes sense to think of those things as “problems to be solved”. I’m not sure I fully endorse either of those assumptions, but the view is still a really useful counterpoint to the short-sightedness of (1) above.
This frame is the one that’s implicitly adopted anytime someone asks about your “10-year plan”, or indeed, anytime you plan something as long-term as a “career”. Organizations such as 80,000 (80K) Hours explicitly advocate for an approach towards identifying a career that addresses important problems:
You have about 80,000 working hours in your career: 40 years x 50 weeks x 40 hours.
If you want to have a positive impact with your life, your choice of career is probably your best opportunity to do that.
That means it’s worth thinking hard about how to use this time most effectively. If you can make your career 1% higher impact (whatever that means to you), it would in theory be worth spending up to 800 hours working out how.
We aim to help you work out how you can best use your 80,000 hours to help others, and to take action on that basis.
In my experience, online discussions about 80K Hours (or related organizations) sometimes get hung up on what kinds of things the organization considers a major “problem area” (e.g., AI risk, engineered pandemics, or factory farming). But it’s entirely possible to apply the underlying framework to any kind of long-term planning about how you spend your time. In fact, I’ve met plenty of cognitive scientists who do view their career in terms of a big-picture problem (e.g., “solving vision”); they usually have a set of reasons for working on this problem that aren’t too different, ultimately, from the decision framework 80K Hours suggests using.
Specifically, many people present a rationale rooted in (roughly) three criteria mirroring the 80K Hours framework: impact (how important is the problem?), tractability (can you actually make progress on the problem?), and neglectedness (is it likely to get solved without you?). Readers will likely notice that these are the same criteria I presented in section (1) above: indeed, you can apply this framework both to short-term decisions and to career planning.
One way to think about this framework is as a kind of algorithm. In theory, you could actually quantify these things for yourself: that is, if you consider the range of possible options, and you situate each option in some three-dimensional space parameterized by these criteria (impact, tractability, and neglectedness, or “ITN”), you can identify the options that reside in the most “optimal” part of that space.
Alternatively, you can simply think of the criteria as heuristics to remember whenever you’re faced with a decision or as you’re thinking about the arc of your career. As an exercise, I assigned subjective ITN ratings to a bunch of my projects recently. It didn’t change anything about what I wanted to work on—that’s really a matter of taste, as I argue below—but it was informative about my own process: for instance, it revealed that I’ve historically over-emphasized tractability, perhaps at the expense of impact. That encouraged me to be a bit more ambitious in terms of finding projects that I think will be important, rather than finding projects I know I can complete.
(3) A matter of taste
There’s much one could say about research taste.
Some people think of it as something that can be good or bad, as in “this person has good taste in research questions”. For me, a more precise rendering casts taste in terms of its degree of attunement, as in “this person has a really well-developed sense of research taste”. Different people will, naturally, be drawn to different kinds of questions or theories—just as different people are drawn to different constellations of flavors—but each individual can work to acquire better self-knowledge about their own tastes and, if they so desire, work to either refine or expand those tastes.
Unlike something like the ITN framework described in (2), taste is (in my view) an approach towards research that can’t be generalized, represented algorithmically, or decomposed into its constituent parts; it is by its nature both holistic and highly individual. That’s part of why I don’t think taste can really be “good” or “bad”: some people will have a taste in questions that better aligns with the rest of their field (and, accordingly, makes them more successful in terms of their number of publications, promotions, etc.), but that doesn’t necessarily make their taste better. We can, however, strive to better understand and express our individual tastes. The motivation for doing so might be something like self-knowledge (it is interesting, and fruitful, to learn what you like and don’t like); it might also be crucial to honing your taste so you can more readily and intuitively identify what draws you to particular research topics.
An example here might clarify what I mean. I’ve worked on a number of projects throughout my research career thus far, but as I stand here with the benefit of hindsight and attempt to make sense of the overall shape of these projects and papers, one thing that stands out is that I’m consistently drawn to projects that question the link between some empirical analysis and the theoretical conclusions drawn from that analysis. This particular taste might be described as an epistemological frustration (a “distaste”) with what I take to be unwarranted claims. This was the motivation for some of my earlier work on the role of efficiency in language evolution: it’s not that I disagreed a priori with the argument that languages are shaped by a pressure efficiency, but I felt that some of the pieces of evidence used to bolster this claim were also consistent with other theories. It’s also the driving force behind much of my work on LLM-ology, which focuses on whether we’re measuring LLM capabilities in the right way and whether our results generalize to a broader population of LLMs.
Of course, many scientists—including myself—are drawn not only by their distastes but by an appreciation of something like beauty: a positive, rather than a negative, tropism. The writer and scholar Emma Stamm recently pointed me towards an interesting study examining aesthetic experiences among biologists and physicists. A substantial percentage of practicing scientists in both disciplines reported regularly experiencing a sense of awe and wonder with respect to their subject of research. Yet the source of beauty varied by individual and by discipline: to cite a particularly illustrative example, some people find beauty in simplicity, while others find beauty in complexity; perhaps some find beauty in both!
The notion of “elegance” in a theory is, perhaps, overstated by some—certainly, elegance is not identical with accurate. But there is something that feels important about the ineffable sense of resonance one occasionally feels in the moment of encountering a particularly elegant theory or explanation. For me, elegance often manifests as something like explanatory insight. One paper that fits into this category for me is Jeff Elman’s 2009 paper “On the Meaning of Words and Dinosaur Bones”3; another is Len Talmy’s 1988 “Grammatical Construal”. Both papers, notably, present a theory—motivated by psycholinguistic evidence in Elman’s case, and linguistic examples in Talmy’s—of linguistic meaning: what it is and how different parts of language contribute to it. Another writer who consistently strikes me with his capacity for insight is William James, who is almost literary in the way he weaves together case studies and introspection to craft a coherent account of something as seemingly intangible as religious conversion.
But that’s just me. Different people will presumably be drawn to different sources of beauty. This is precisely my point: it’s not that some theories (ideas, results, etc.) are more beautiful than others, but that we can learn to recognize what we find beautiful and why, and that alone is a useful and illuminating insight about ourselves and the way we choose to spend our time. I’m not really sure how one develops this sense of taste—but I do think that taste, perhaps more so than any other aspect of experience, is not something that can be arrived at via shortcut, and it is possibly not a destination at all.
Another version of this challenge might be framed in terms of journalism or public-facing writing more generally: what should you choose to write about?
Again, from the journalistic perspective, maybe this could be cast in terms of “your next article”.