Thursday, September 19, 2019


Part 1 of a series on choosing your research topic


I might be guilty of stereotyping here, but I suspect relatively few readers of this blog would consider themselves fashion-conscious. Do you go to fashion shows? Regularly read fashion magazines? Discard last month's clothes in favor of the latest trends? That's not something I normally associate with the crunchy-granola environmentally-conscious caricature of an evolutionary ecologist. [if you do, my apologies for stereotyping]

But we do follow fashions in our own way. Science too has its academic fashions, and in particular I'm thinking of fads in research topics (see Fads in Ecology by Abrahamson Whitham and Price, 1989 Bioscience). My goal today is to contemplate the role of fashions, for good and ill, and what you should do about them when planning your own research. This post is inspired by a discussion I co-led yesterday with Janine Caira, with our first year Ecology and Evolutionary Biology graduate students at the University of Connecticut. The focal topic was, "How to choose a good research question".

A core rule I tell students is: when choosing a research topic you must have an audience in mind. Who will want to read your resulting paper? How large is that audience, and how excited will they be? If the audience is small (e.g., researchers studying the same species as you), you aren't going to gain the recognition (citations, speaking invitations, collaboration requests) you likely crave and which will help your career progress. If your audience is large, but you are doing incremental work that will be met with a widespread yawn, that's not very helpful either. Ideally of course you want to present something that is really exciting to as many people as possible. But, the more exciting and popular it is, the more likely it is somebody has gotten there first.

Which is what brings me to fads. A fad is defined (in Google's Dictionary) as "an intense and widely shared enthusiasm for something, especially one that is short-lived and without basis in the object's qualities; a craze". Intense. Widely-shared. And with at least a hint of irrational exuberance (a reference to former Federal Reserve Chairman, Alan Greenspan).

Fads happen in science, with a caveat that they aren't always irrational exuberance: there are research topics that genuinely have value, but which nevertheless have a limited lifespan. I'll give an example: When I was a beginning graduate student, Dolph Schluter [for whom I have immense respect] had recently started publishing a series of papers on ecological speciation, along with his Ecology of Adaptive Radiations book which I heartily recommend. The core innovation here was that ecology plays a role in (1) driving trait divergence between populations that leads incidentally to mating isolation, and (2) eliminating poorly-adapted hybrids. Both ideas can be found in the literature of course, few ideas are truly 100% new. But what Dolph did was to crystallize the idea in a simple term, clearly explained, and solidly justified with data, making it compelling. And suddenly everyone wanted to study ecological speciation, it seemed to me. There was a rapid rise in publications (and reviews) on the topic. Then at a certain point it seemed like fatigue set in.  I began encountering more conversations that were skeptical: how often ecological speciation might fail to occur, where and why is it absent, how common is it really. At one point, an applicant for a postdoc position in my lab said he/she wanted to work on ecological speciation and I couldn't help wondering, okay that's interesting material but what do you have to say that's new, or is this yet another case study in our growing stockpile of examples? And I think I wasn't alone: the number of papers and conference talks on the topic seemed to wane. Its not that the subject was misled, wrong, or uninteresting: I'm not saying it was irrational exuberance. Just that the low hanging (and medium-hanging) fruit had been picked, and people seemed to move on. To drive that point home, below is a Web of Science graph of the peak and maybe slight decline in the number of publications per year invoking "ecological speciation" in a topic word search. Interestingly, total citations to articles about "ecological speciation" peaked just three years ago, after a steady rise, and the past two years showed somewhat lower total citations to the topic.
Ecological speciation articles by year

Meanwhile, other topics seem to be on the rise, such as "speciation continuum" (next bar chart), which Andrew Hendry, Katie Peichel, and I were the first to use in a paper title in 2009 (it showed up in sentences in 2 prior papers) and was the topic of a session at the recent Gordon Conference on Speciation [still not anywhere near a fad, just 72 papers use the term, and there are reasons to argue it shouldn't catch on]
Speciation continuum
And of course "eco-evolutionary dynamics" and its permutations are fast-rising and very popular these days:
Eco-evolutionary dynamics, total citations

Life cycle of a scientific fad:

1) Birth: someone either has a great new idea, or effectively re-brands an old idea in a way that makes it catch on. Sometimes an old idea gets new life with a clever experiment or model (e.g., both reinforcement and sympatric speciation were old ideas, that caught fire in the early 1990's and late 1990's respectively after new data or theory rekindled the topics). The simplest and least valuable way to start a new fad is re-branding. Don't do this, it sometimes works but really annoys people. Take a familiar idea that's been in the literature for ages and give it a name, or rename it, and pretend it's an innovative concept.
2) The sales pitch. For the idea to become a fad, someone needs to really hit the streets (or, printed pages) and sell the idea. Giving lots of talks, writing theory/empirical/data papers in journals where the idea is seen.

3) People get excited, and start thinking what they can do to contribute. There's a lag here, where the idea spreads slowly at first, then accelerates as people start to find the time to run models and write papers. For empiricists, there's a lag while people design experiments, get funding, do the experiments, analyze and write. This takes years, and doesn't all come out in one burst, so there's an exponential growth phase. This is a good time to get in on the topic. Personally, as a second year graduate student I read the Dieckmann & Doebeli 1999 and Kondrashov & Kondrashov 1999 Nature papers on theory of sympatric speciation, and immediately started designing lab and field experiments to test their model assumptions about disruptive selection and assortative mating, work that I started publishing in 2001, peaked around the mid-2000's, and touched on only occasionally since then. In short, I was part of the rising initial tide, after their theoretical advance rekindled the topic. In the graph below on "sympatric speciation" papers you can see an uptick after the 1993 paper by Schliewen et al on Cameroon crater lake cichlids, and again an acceleration after 1999 theory papers. I came in right in the middle of the wave, and published my AREES paper with Ben Fitzpatrick in 2007, right as it crested and soon began to fall off again.
Sympatric speciation

4)  Fads don't go away entirely, usually. Both Ecological Speciation and Sympatric Speciation, for example, declined slightly after their peaks (see graphs above), but are very much still with us. Because they have value. But the initial excitement has passed, the honeymoon is over.

5) Fall from favor. At some point, it becomes increasingly hard to say something creative and new about a topic. Not impossible, mind you. And so grant reviewers and journal editors become increasingly skeptical. Journals that favor innovative and flashy results get harder to publish in. I hit this, sort of, when I briefly toyed with gut microbiome research: we studied how natural variation in diet among individuals affected the gut microbiome. Science reviewed it, and the Editor was enthusiastic but wanted some more manipulative experiments to prove a core claim of ours in a controlled setting. It took a year (of postdoc salary, time, and $10,000 in sequencing) to get the data the Editor asked for. It confirmed our initial claim, beautifully. But in the intervening year, gut microbiome research had become increasingly saturated. To get a Science paper you now needed molecular mechanisms, not just documenting that phenomena occur. The same Editor who had expressed enthusiasm before, now said it wasn't interesting enough. I'm not complaining (too much), but use this to point out that when you hit a fad at its crest, standards of publication become more stringent and its harder to impress or surprise.

6) Rebirth. Some fads come in waves. Think Bell Bottoms. Or jazz swing-dancing. But I'm wrestling with finding a good example. Lamarckian evolution seems a safe one, or even sympatric speciation which in the 1960's Ernst Mayr said was dead, but like the Lernean hydra, it would grow new heads again (which it did).

Avoid or embrace the fad?

Given that fads exist, what should you do about them? On the one hand, they represent a ready-made audience. This is the hot topic of the day, and publishing in that area will surely draw many readers to your work, right? Perhaps. That depends on when you are coming in on the fad. Here are some options:

1) Start a new fad. Come up with an idea so brilliant and widely appealing that many people pile on and build on your work. This is a guaranteed ticket to fame, if not fortune. Of course, it rarely happens and you have to have some combination of exceptional brilliance and luck and good salesmanship. So, don't bank on this approach: a lot of attempted new fads quickly become failed fads (see photo below). 

2) Catch the wave: Contribute to a fad in its early days. This requires reading the current literature very closely and widely, and acting quickly on great new ideas as they appear in print (or, in conference talks, etc). You still need a good intuition for what people will find exciting in your field, but less initial creativity than option (1). This is more or less where I came into the sympatric speciation field, with a couple of somewhat skeptical theory papers, and some somewhat supportive lab and field experiments on disruptive selection. 

3) As a fad nears its peak, the audience is now very large, but truly new ideas are becoming more and more scarce. Still, there are still usually new directions you can take it. Sure we know X and Y are true, but what about Z? Be careful though: as fads near their peak, your audience starts to experience some fatigue with the topic and are more likely to say, "oh, its another paper on gene expression, yawn". Might be a good time to avoid. Or, do a meta-analysis or review that synthesizes the topic, wrapping it all up in an easily accessible package.

4) Be contrarian.  Sure, this fad thing exists. But how common is it? How strong is its effect size relative to other things we might get excited by? Might we be over-interpreting the evidence or being too simplistic? One of the reasons fads go away, is that people shift from being excited that a phenomenon even happens, to taking a more measured quantitative and objective view. Sure, there's parallel evolution, but are we just cherry-picking extreme cases and ignoring the bulk of traits and situations where evolution is less parallel? 

5) Merge fads. There used to be these TV advertisements for Reeses Peanut-butter Cups. Two people walking down the street, one eating peanut butter with a spoon (really??? who does this?), the other eating a bar of chocolate. They collide, and discover their combined food is so much better than either alone. Some great scientific papers are like Reeses Peanut-butter cups. They take two familiar subjects and merge then in an unfamiliar way. Two fads put together can make a super-fad. 

6) Revive old fads (zombie ideas). Old fads never truly die, they just hide away in a quiet steady tick of more papers that aren't making a big splash anymore perhaps. The key thing is, their audience never truly went away, they just reached a point where they moved on. But like many failed relationships, you often never truly stop loving your ex. So, if you can locate a former fad and give it new life, you have a ready-made audience and a small field of competitors. This is especially easy to do when a previous fad ran out of steam because people in the old days lacked analytical tools that we have now: sequencers or flow cytometers or Bayesian statistics or whatever. If you can apply modern lab or computational technology to an old fad, you might make fundamental new progress, on a widely-known topic. Doing this requires reading your history, to know where the good zombies are buried. When I was a graduate student, I spent a summer reading Ernst Mayr's Animal Species and Evolution. Its a seriously dry book, packed to the gills with case studies and examples, and ideas. Many of these were abandoned, for various reasons, and are just waiting around to be exhumed, re-examined in light of new perspectives and tools, and maybe re-animated.

I'm sure there are more variants on this theme, but I think the point is made:  fads are a great way to make your name in academic science. They are also a trap, if you hop on the band wagon just as it goes over the cliff into obscurity. To know which is which, you need to read read and read, and go to conferences and talk and listen, to get a sense for the pulse of your field.

Now, your turn: 

What do you see as passed or passing fads in your field? How can we know if something is a fad-to-be and get in on it early?

1 comment:

  1. Interesting piece. Here's what I was wondering as I read it: are fads good or bad for science? Of course arguments can be made both ways. Good for science: by focusing attention of particularly interesting/new/timely questions, a fad pushes a field to make major advancements quickly. Bad for science: a fad causes other worthwhile research areas to be unjustly neglected, results in an overproduction of quickly-thrown-together work in one area much of which might be of low value, and then causes people to burn out on a topic that might, in fact, still deserve continuing attention – just not at the level of intensity that a fad brings. So there's the career-focused angle that you take here, of "fads exist; how do I leverage them for my professional advancement?", but for more senior researchers who have the luxury of making choices without such a focus on career advancement, there's also the angle of "fads exist; should I encourage them as beneficial to the field, or oppose them as destructive to science, or somewhere in between?" The same question might apply to journal editors too (if a journal is in the luxurious position of not having to worry too much about maximizing citations, and can afford to think about what will produce the most actual scientific advancement). Thoughts?


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