Dafs asked:

“…I read “tenure hacks” that you reviewed awhile ago and I am wondering what you think about staying in a niche area — after you have tenure.”

This is a great question! It really depends on the person. That first sabbatical leave after receiving tenure is sometimes (often?) used for reflection on the long-term career trajectory.

There are people who never really veer far from their original niche. The upside is that they might become the unparalleled and thus the go-to expert for certain problems. The common downside is that people stop caring and the funding for the niche runs dry, and they end up not being able to support students or postdocs; this is a common mechanism for “research deadwoodification.”

One of my colleagues, going into their first sabbatical, said they were getting bored with the topics and that it was time for a change. Yet, as they emerged from the sabbatical, they kept doing the same thing. The second sabbatical came and went, and they still work on more or less the same topics, but have since taken on significant college-level administrative duties. I wonder if this boredom with  the research topic had anything to do with administrative ambition; perhaps the administrative ambition was always there. Or maybe the colleague decided they didn’t have very much scientifically to give in the broadest sense and decided on a different career track.

I suppose it somewhat depends on how narrow your niche really is and how insular the corresponding communities are. There are relatively broad subareas within which people move freely, without scientific penalty. Certain subdisciplines of applied math, statistics, computer science, and theoretical physics seem to fit this description, as people successfully tackle a variety of problems and are praised for intellectual vigor and versatility, rather than looked at with suspicion for overstepping the boundaries of their expertise. It appears to me that changing a niche objectively becomes harder when you do experimental work, because the cost of equipment, materials, and supplies is a deterrent, and it is unclear how one pays for a drastic shift in focus (and the associated drastic costs). Having a gigantic operation and abundant funding likely help and enable great breadth (you simply hire postdocs who already know how to do what you want to do). In general, being a superstar in one field helps, both financially and during peer review, when trying to shift gears.

I personally like variety. I probably spread myself a bit too thin early on, which in hindsight could have been a disaster at tenure time. It worked out, as I now have years of experience and publications in several fairly different subareas, so I am in a good position to seek funds for cross-cutting topics; still, I do occasionally get annoying comments in reviews that I don’t have expertise in this or that even though I have published on those topics. I still always look to broaden because I get bored. I enter a new field, there is the scary but invigorating learning curve, eventually we say what we have to say, and a few years later I think it’s time to move on. Perhaps that makes me a shallow scientist — a jack of all trades, a master of none — but I do know a little or not so little about a lot of things, and from such a vantage points you sometimes see connections that are harder to grasp when you dig deep in one place.

There is one topic on which I have worked on and off for years, usually with fringe money (e.g., an internal year of fellowship for a student here, a TA-ship there, a few months of freed-up money after another person graduated early). But now I see that I have years of experience and a number of papers that people cite, so maybe I finally feel like maybe I can say that I actually work in that field. In contrast, there are people in the same field who have been working on nothing else for decades.

So what’s the moral of the story? There is definitely such a thing as too small a niche, where both the ideas and money run dry on timescales much shorter than one’s career. But if you have a topic you enjoy, where you keep mining and getting ever larger and more exciting gold nuggets, and you keep getting funding for the work, by all means keep at it. You don’t absolutely have to change topics. For many people, the change is gradual and organic, as they follow the questions that arise in research.

There is no catch-all answer, other than that it depends on your personal work style (are you more of a scanner or a deep diver?), funding climate and institutional support, the vitality of the field you are in (running dry or sprouting new research directions), and how insular the communities in the broader field are. In my opinion, there are far too many boring (committees) and depressing (funding rejections) parts of this job, that it is critical to follow your bliss and where the curiosity leads you, otherwise what’s the point?