On specialization: don’t research your way into obscurity


A current conversation about model systems and the benefits of being a scientific specialist or generalist has been interesting, and I thought I’d join in. (This post was written for a while, but now’s a good moment to actually share it.)

Here’s my main point : Becoming a specialist on a narrow topic or taxon is a bad idea, because it narrows your opportunities and decreases both your visibility and your impact. If you’re in a position to choose your research trajectory and degree of specialization, I have two specific prescriptions near the end of the post.

When building a research program within teaching institutions, I’ve seen junior faculty advised by senior colleagues to avoid competing with big research labs. They are advised to find a specialized topic, not subject to competition, and develop expertise. For example, I’ve seen people whose entire research career, at a teaching institution, is built on the phylogenetic reconstruction of a single genus.

The notion behind this strategy is that you can be the world expert in something if nobody else is studying it. This route can allow you to retain a niche in academia, even if you are busy enough teaching that you can’t penetrate a more broader or more mainstream research agenda.

This sounds like a horrible idea.

If you specialize on an obscure topic that nobody is interested in studying, that means that you’ve become an expert in a mostly useless topic. What good is that?

If you are convinced that your particular obscure field should is truly important, and that the whole world is wrong, then that’s a different matter. If you think that understanding the detailed phylogeny of a single genus is important because of the unrealized significance of this group and the broad and general lessons to be learned from this model taxon, then fine, go ahead and spend your career working on it. However, if you choose a specialization for the purpose of defending a narrow niche, then you’re not allowing yourself the academic freedom that produces the best scholarship. And, you’ve intentionally chosen a route to obscurity.

Let’s just say that your obscure specialty suddenly matters to everyone? Let’s say that your model genus simultaneously emerges as an invasive species, produces a cancer-curing chemical and is the secret to carbon-free energy production. Are you going to have a great impact? No.

You’ll get more attention at first, but then you’ll then be shuffled back into obscurity when the big names in the field move into your pet taxon. Then, you won’t even own your little niche anymore, and your work will be seen as even more obscure.

Here’s a true anecdote: I once worked with someone who worked in a tiny niche, without collaborating. Coming up for tenure at a teaching institution, this person focused work on a single niche project over a few years. Shortly after the project was finished, less than a year before turning in the tenure dossier, this person was scooped by a bigger lab. This bigger lab just knocked out this work as a side project with some spare time. This unfortunate choice to overspecialize, without collaboration, meant that this person came up for tenure short of research expectations.

You won’t be a famous scientist working at a teaching institution. So, if you’re going to be a successful scientist, you need to be productive and successful one without the fame. Success in research is often based in collaboration, and people won’t be seeking you out for your narrow expertise in an obscure topic – they’ll be seeking you out because you are good and have something useful to offer for research on an existing question of interest.

Why would someone work in an obscure niche? Maybe it could be a personal passion, which would be a great reason, just like any other hobby. Other than that, the only reason I can think of is that a noncompetitive niche enables someone to continue to consistently publish a large number of papers that few people read. Some have made the argument that working on an obscure topic is the only reliable road to a position in the academic community, for those who are working in teaching institutions. It’s the road to being recognized as a scholar on your campus, but that’s not our real academic community.

Doing this work on an obscure topic buys you a place at the table. That might be true, with a caveat: Working on minutia buys you a place at the kiddie table.

What is a good attitude towards developing a research program at a teaching institution? It should take advantage of the fact that the productivity or prestige of your research program isn’t so important to your institution. I agree with Chris Richardson of Young Harris College, who uses his job at a teaching institution to give him the freedom to do research on anything that interests him:

There is… much less pressure on me to be the expert in one particular niche, leaving the research questions I can pursue much more open.

What is the best approach towards the generalization/specialization continuum as a researcher at a teaching institution? I have two specific prescriptions:

  1. Do whatever you want! Be free! Use the freedom that have.
  2. You’re best off if you general work on a diversity of questions, but within a framework that allows you expertise that will be of collaborative utility.

I’m not an ideal example, but at least I’m familiar with myself. Nearly everything I do involves ants. Moreover, it’s on one particular location that’s only 15 km2 in area. It’s easy to argue that this is obscure. However, the questions that I have asked include behavior, community ecology, some ecosystem ecology and a little chemical ecology sprinkled in. I have a set of experimental techniques and data that allow me to have specific, and long-term, information that is very difficult to acquire in any system. So you could say that I only study ants, in this one tiny place. Or you could say that I’m a generalist who works on all kinds of questions, with this one particular system.

What has this approach done for me? I’ve chosen the place where I work carefully, and it is a place where a lot of other people work. The kinds of information that I have generated can be useful to others, and my experience allows me to be of substantial use as a collaborator. Actually, I’m not even close to being the main expert of my taxon of choice at my field site. I am, however, a guy who works there consistently and broadly on a variety of questions, and is prepared to engage with collaborators on new questions.

I’m not required to follow a path that necessitates continuous external funds, marketing my doctoral students and publishing well every year. This is the ideal academic job – I am not required to satisfy anybody with my research program, other than myself. Hopefully the research will be broadly useful to all, but I can design and run it as I wish, based on the funding, timescale and focus that suits my needs.

I’m not wedded to my study system, nor to the single place where I’ve conducted most of my field-based research for my career. But, it works for me, and I really enjoy it, and this depth of experience in this one system and location gives me an avenue to ask lots of questions in all kinds of fields that I wouldn’t be able to do if I switched to a different taxon or location with which I was less familiar.

So, I’m a geographical and taxonomic specialist, but a conceptual generalist. To me, this is the most fun way to do science, and it lets me give great opportunities to students as well as to collaborators. I think this approach merges the benefits of generalization and specialization but minimizes the drawbacks.

7 thoughts on “On specialization: don’t research your way into obscurity

  1. interesting post, and good advice.

    As an aside, reconstructing the phylogeny of a single genus, depending on the genus, can be a substantial research focus. I did my PhD at a research school, and my supervisor’s focus was just this. And she was doing and continues to do high quality work.

    It seems to me ecologists are quick to point to taxonomy when looking for examples of trivially obscure science. Our work, and grant applications, get peer reviewed just like ecologists. It may not seem valuable or relevant to you. But how much ecological work makes an impact in other disciplines?

    Sorry to jump on such a small point in an otherwise useful and nuanced post! Some of us get a little sensitive to ecologists picking on our science.

    • And I’m the guy that invented Taxonomist Appreciation Day!

      19 March! Put it on your calendar!


      Systematics is the foundation of everything biologists do! It is possible that certain lineages can be important, valuable, tricky and hold important lessons, even within a genus. Like I wrote, If you think that understanding the detailed phylogeny of a single genus is important because of the unrealized significance of this group and the broad and general lessons to be learned from this model taxon, then fine, go ahead and spend your career working on it. (That sounds flippant, I see in hindsight, but I try to avoid sarcasm in print.) It would be great for a career, if there are broad and general lessons to be learned, which there can be.

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