Small labs should avoid theoretical bandwagons. It’ll make it hard to get money, publish and do good work effectively.
In an earlier post, I described two categories of research: the development of new ideas, and the testing, shaping and fine-tuning of these ideas.
I said I didn’t like either of the categories. I’ll explain that next week, but to get to that point I need to explain how big labs are designed for bandwagons, and how labs at teaching institutions should avoid designing their work to address bandwagon theories.
A bandwagon — as I use it here — is any theory, topic, or issue that lots of people are working on simultaneously. What do I think are some bandwagons at the moment? It’s easy, just pop open a journal and look at the table of contents! In ecology and social insects, my two main fields, here are a few that are at some point in the bandwagon boom-and-bust cycle: functional traits to understand community structure and assembly; genomic approaches to understanding the social regulation of development; models of geographic range shifts in response to climate change; physiological and genomic mechanisms of task allocation. (You could also throw in arguing about group selection, but that’s more about yelling than data.)
I’m not saying that the scientific community doesn’t need this work to happen. All of these topics are very interesting, and people have chosen them because they’re ripe for discovery and progress. It’s not a bad thing that these topics are bandwagons. When great ideas come along, we need people to work on them, including both disagreements and points of consensus. This is the standard practice of science.
It’s so much the standard practice of science, that labs at research institutions are engineered to thrive while working on bandwagons. Race cars are built for speed, thermoses are designed to keep your drinks hot, and many big research labs are designed to produce bandwagon research. (Not all big labs do, but they can be easily engineered to do so if this is the goal of the PI.)
If you’re running your own small lab at a teaching institution, there are a number of major strategic disadvantages from working on the same questions as big labs. These are disadvantages because they make it harder for the lab to get grants, publish papers, have a visible research profile, develop collaborations and provide the best opportunities for students.
No matter what you do, you won’t be perceived as the primary expert on the bandwagon topic. There will always be someone who is considered to be the authority, who is more productive on the topic. This person will have a whole lab working alongside them on the same topic. Moreover, this person’s name tag at conferences will have the name of big of a research university next to their own. Does this perception as an expert matter? Sure it does. This kind of perception enables you to do better science and gives better resources for your students.
Big labs can mobilize to jump on bandwagons quickly. They can turn on a dime by having a new dissertation start on the project, or assigning a postdoc to it. (You’re thinking, dissertations don’t start overnight?! Compared to the timescale of when I start and finish projects, they do. Tomorrow is a story about a quick project done in 2008 but was published this year. That’s par on my course. The manuscript I’m editing today has has had all of the data assembled on my hard drive for seven years. And I’ve been thrilled about it the whole time, too. And – get this – it’s still not stale. It’s actually ripened.)
You don’t want to work on a specific aspect of a project when other bigger labs will get to them quickly. Moreover, big labs will work so quickly that they will exhaust it before you get finished. In ecology, for example, thank goodness I didn’t work on the mid-domain effect myself or I would have entirely missed that wave before I even submitted my first paper. I would like to work on functional traits in ants, as the ideas seem interesting, but the same thing will happen to me if I do that. My paper would be passé by the time I tried to publish it.
Big labs need big funding. Theoretical bandwagons are the things that attract dollars. They can be sold as “transformational” research that NSF is seeking to support. Most of these potentially transformative projects will end up in the dustbin of history, and a small fraction will result in big change. If you’re a big lab and you need to pay for people, then you better hop on board! If you don’t, you’ll have trouble keeping staffed. If you’re top notch, you an create your own bandwagon. But if you catch it in the first couple years, then you can still get in there for one grant cycle, or maybe even two. Following the same principle, bandwagons are horrible for small labs because they can never compete with these big labs that are putting in proposals on the same question. They’d never survive a side-by-side comparison once you put the biosketches up against one another. Of course they’ll fund the lab that they think will get 10-20 papers out of a project when they think you’ll only get a few out of it. So stay away unless you have the record to show that you can beat the top labs riding the same bandwagon.
To be clear: I am not suggesting that scientists at teaching schools specialize on an obscure topic that nobody is interested in, that can be mined for a series of novel but inconsequential publications.
I not suggesting that you stay fully clear of theoretical bandwagons under all circumstances, but only that if you hop on it should be with a big lab that is ready to roll. You also could take an existing project of yours and sell it this way, if you wish, though that will shorten its shelf life.
Next week, I’ll share a taxonomy of research goals, which will explain how I think you can do novel and truly meaningful research without chasing theories-of-the moment.
There are exceptions to every generalization of course. My undergrad advisor (whose lab comprised one former student turned academic and collaborator, and any undergrad honors students he happened to have) wrote the Am Nat paper that kicked off a massive wave of research on adaptive plasticity in anuran larvae (Smith and Van Buskirk 1994 American Naturalist). And my own lab, like those of many Canadian ecologist, comprises a small number of grad students, each doing their own thing with maybe one undergrad assistant in the summers or a bit of part-time undergrad help during the academic year, and with funding from a single, modestly-sized NSERC grant. And while I can’t speak for anyone else, my own approach and the approach of my students is to just try to identify good questions, and good ways of addressing them. Very different from identifying popular or “hot” questions, of course–good questions may or may not be hot, and hot questions may or may not be good. Now, if that good question is also hot, then sure, you have to think about whether you’re going to be able to make a worthwhile and distinctive contribution to that rapidly-growing body of work. But that’s something I think we’ve been able to do, in part because a lot of our work is in model systems that let us do different sorts of experiments and collect different or better sorts of data than most other people can collect.
Great point – the venn diagram of ‘good questions’ and ‘hot questions’ features overlap, and it’s possible to focus on good questions regardless of how hot they are at the moment. There are plenty of good – and theoretically based – questions that aren’t being worked on. What I find even more exciting is trying to find that question – learning new information about the world that enables the creation of questions. Unfortunately, that’s “merely descriptive” or just knocking a system to see who answers. But it floats my boat.
Another angle to consider is not so much staying off of theoretical bandwagons, but to find the parts of the bandwagon that need work – the sometimes smaller, more detailed questions that those riding the bandwagon often ignore, whether unwittingly or by choice. Many of these are still juicy, meaningful questions, and answering them can often can have an impact on the field. It can also show your students that the originality and thoughtfulness of a question matters as much as the specialized technical knowledge of the “expert.” Really good questions, bandwagon or not, addressed with a well-designed scientific study are like those “old” data on your hard drive: they never go stale.
Right-o, Drew. Little ignored aspects of a big question are often the really interesting and long-lasting ones. Maybe that’s a way to ‘ride the bandwagon’ without getting trampled by it. My rule when doing something is, “will someone 20 years from now still be interested?” If the answer is no, I try to stay away.