The bandwagon effect is when people believe or do something just because lots of other people believe or do it, independent of other reasons for believing or doing it (such as empirical evidence or logical argument). Like every science (e.g., astronomy, information theory, quantum physics), ecology has bandwagons. Probably every “hot” topic in ecology, or any science, has a bandwagon-y element to it, because some of the people who work on that topic choose to work on it precisely because it’s “hot”. Indeed, I think it’s difficult or impossible for a topic to become really “hot” unless it’s also a bandwagon, even if there are very good independent reasons for pursuing that topic.
Note that choosing to work on a “hot” topic because it’s “hot” need not indicate a researcher who is a “copycat”, or who lacks ideas of his own, or is just pursuing whatever idea he thinks will get funded, or anything like that. Rather, it’s a natural outcome of how many graduate students (and some others) choose their research projects. When choosing a research project, aren’t you supposed to read widely, see what’s going on in your field and related fields, and identify some important general question, approach, or idea that you can address/apply/modify/build on in your own system? I don’t think that’s a bad thing–it’s a good thing, mostly–but for better or worse, one effect of that way of choosing a research project is that you’re rather likely to jump on a bandwagon.
A scientific bandwagon is a positive feedback loop, a sort of Allee effect or runaway process. How does that process get started? What determines whether or not interest in a topic grows to a tipping point, at which the bandwagon effect takes off? Maybe (hopefully!) interesting, worthwhile, important topics are more likely to reach that point on their merits, so that bandwagons are also likely to be those lines of research with the greatest intrinsic merit. I actually do think that’s part of the story, which means that calling something a “bandwagon” can be a complement.
But intrinsic merit surely isn’t a complete explanation for what gets bandwagons started.* For instance, in my totally unresearched and off-the-cuff opinion**, I think bandwagons in ecology tend to be associated with new research approaches that are, or appear to be, very easy to apply very widely, and which are initially presented by prominent people in a prominent venue. The approach becomes a sort of “recipe” which lots of people try to follow, because who wouldn’t try out an easy-to-follow recipe for a delicious (scientific) pie, especially one first presented by a great chef in the scientific equivalent of Bon Appetit?*** Ecology is hard, so we’re always on the lookout for recipes or shortcuts that promise to make it easier. One example is biodiversity-ecosystem function research, especially that very prominent part of it concerned with the total biomass or productivity of random combinations of different numbers of species. In their most basic form, so-called “random draws” experiments are easy to do, and they were initially advocated by David Tilman in 1996 in Nature. Another example is probably phylogenetic community ecology, specifically the questions, and the approach to answering them, laid out by Webb et al. (2002).**** A third example is probably the use of species-abundance distributions to try to test neutral theory.
At some point of course, bandwagons stop and their riders abandon them. No runaway process can continue forever (although biodiversity-ecosystem function research is giving it a good shot!) Once the low-hanging fruit is picked and the novelty wears off, there’s less good reason to continue riding the bandwagon, and it becomes harder to publish slight variations on the original recipe. At that point, some ecologists (perhaps those who got on the bandwagon for good reasons, rather than because everybody else was getting on) get off.
But until that happens, bandwagons are hard to stop. Off the top of my head, I can’t think of any big bandwagon in ecology that was stopped “prematurely”, for instance because outside criticism convinced those riding the bandwagon to get off before they would otherwise have done so. Maybe the null model wars, which (temporarily) stopped the use of null models and other observational approaches as a means of demonstrating interspecific competition? I’ll be curious to see if recent attacks on phylogenetic community ecology from Losos and Mayfield & Levine have any obvious effect on the trajectory of this bandwagon.
Probably the best reason to think about former and current bandwagons is to gain insight about future bandwagons. So what do you think will be the next big bandwagons in ecology? MaxEnt seems to me to be one candidate, but it came in for a lot of strong (but very constructive) criticism very quickly, which may prevent it from being treated as a “recipe” which lots of people try to follow (see, e.g., the recent special feature in Oikos). Then again, random-draw experiments in biodiversity and ecosystem function research famously became a bandwagon despite, or perhaps even because of, stringent criticism, some of it published in Oikos (Aarssen 1997). Addressing the criticism became an additional motivation for jumping on the bandwagon.
Thinking about former and current bandwagons also helps us think about bandwagons that might have been. Are there lines of research that you’re surprised haven’t become bandwagons? Even if they deserved to become bandwagons?
Really looking forward to hearing comments on this one.
*fn 1: Because if it was, everything I’ve ever done would’ve started a bandwagon! (just kidding)
**fn 2: Sorry, but if you want research and careful thought you’ll have to read my papers. This is a blog.
***fn 3: So…much…pie…metaphor!
****fn 4: The easy availability of online genetic data and software tools for building phylogenies really helped get the phylogenetic community ecology bandwagon started. Which may be a good thing, a bad thing, or somewhere in between, depending on your views of the intrinsic merits of this bandwagon. New datasharing and software tools, designed to make it easy for anyone to apply a new research approach in any context, aren’t necessarily an unmitigated good. Taxonomists are fond of joking that “Nothing is so dangerous as an ecologist with a dichotomous key.” But an ecologist with an R package can be pretty dangerous too.