On my desktop sits a file, as a reminder. It’s the log of a Skype text chat dated 24 October 2007.
My desktop isn’t usually tidy, but this file always sits there in a corner. I haven’t read it in years, but its existence is, in itself, a reminder.
This article is third in a series of four. A couple weeks ago I wrote about whether or not we should try to develop new theories or to test existing ones by hopping on theoretical bandwagons.
Last week I wrote why theoretical bandwagons are good for, or at least well suited to, big labs and that small labs should avoid them. (You might want to read those over, if you haven’t yet, before reading the present post. Or not. Your call.)
This week, I’m explaining the kind of research that I choose to do in my own small lab.
This chat took place with a deep friend of mine as we both were undergoing career transitions, both of us starting out in new (and radically different) faculty positions. (It’s great when your friends are your role models, and when your role models are your friends, even if you only see one another in a long while. It’s not too often that you connect with others whose values and priorities are well calibrated to match your own, and it’s a pleasant confluence.)
I had just moved to a new position, back to my hometown. This change involved a massive shift in pretty much everything. I was wondering what kind of questions I should be pursuing, and how I should go about it. My friend was settling into a tenure-track position at a research institution and his lab was growing exponentially.
We were wondering what I was going to work on next. At this point, I wasn’t sure. I had a number of big questions that I wanted to tackle, each of which would involve a major direction for my lab. Up until this point, I had been doing a series of one-off projects (which essentially is what my dissertation was as well).
So, I threw out a bunch of ideas. I want to work on X, I want to work on Y, and Z looks interesting too. I said I didn’t want my work to get lost as ephemera, addressing theories-of-the moment.
Then, at the same moment, we independently stumbled on the term that describes the work that I enjoy most, and also has had the greatest impact.
My best work has happened whenever I’ve found some little natural history curiosity that has piqued my interest, and then I designed an experiment (observational or manipulative) to tinker around with the system to figure out what’s going on. It was my doctoral advisor who first introduced me to “experimental natural history.” (Sorry about the paywall, damn JSTOR)
This leads to both the stuff that is most cool, interesting, and in the long term useful to other people. I think that good science happened because my approach was most likely to lead to discovery, even if discovery was not the goal.
Research is supposed to result in new knowledge.
What are the odds that you’re going to make a big discovery or formulate a grand theory as long as you’re working on the same ideas that other people are? How much are you pushing the frontiers of science when there are other people out there doing the same thing? If you’re working for a specific applied aim – an HIV vaccine, cancer prevention, et cetera, then I can understand that a massive push in one direction, like against a two-ton piece of stone, is what can make the stone move.
I’m not in the business of inventing vaccines for rapidly evolving viruses or building pyramids. I’m doing basic research. I’m just trying to understand how the world works. There is so little that is known, that I want to mine into directions that that are entirely mysterious. The world is still fundamentally mysterious.
I posit that there are two distinct philosophies that scientists have about the nature of our knowledge, with little middle ground. On one side are people who think that we have learned a lot in the fields that we have studied, and that research is filling in the gaps and discovering new fields that we have yet to understand. On the other side are people who think that we are still vastly ignorant about the world, and even the things that we have studied really heavily remain mysterious and what we think we know may in fact be wrong.
Is this a fair dichotomy? Does one of these describe you or do you fit in the middle somewhere?
I’m in the latter group (or at one end of the spectrum if it’s not a dichotomy). I suspect that a number of ecologists might fall into that group as well. For all the work that we’ve done, we’ve only scratched the surface, and that surface is probably deceiving. Some classic major concepts, such as “competitive exclusion,” are so simplistic that they don’t even begin to describe nature.
The one thing that students seem to learn in school about evolution is that Lamarck was wrong, and this lesson comes with a certain example involving a giraffe. It’s taken us a couple centuries to figure out that, to a certain extent, Lamarck was quite right about the inheritance of acquired characteristics after all. He just didn’t know the mechanism was epigenetic, just as Darwin wasn’t aware of the particulate inheritance mechanisms described by Mendel. Jerry Coyne addressed this a score of moons ago.
In short, some things we think we fundamentally understand, we really don’t. This is particularly the case for complex phenomena that are explained by theories requiring mechanisms that can’t be readily measured in nature. Natural selection is very straightforward and observable, and we have that one locked down. But many more intricate concepts in ecology? I wouldn’t buy stock in them.
If your research program is oriented towards testing theories, then you’re less likely to stumble on a new perspective.
When I design experiments, I “tinker” with natural systems by tweaking them in small ways to see what happens. I do this because I find something that’s curious to me, and I want to understand what’s happening in that system. I don’t pretend that what I find will answer a grand theory or unify different branches of our disciplines. I just want to get a little answer about a little thing that’s curious. My suspicion, that might approach something resembling belief, is that this kind of work will help us learn more about the world than most theoretically-driven research. I think that most of our major advances came from this kind of approach as well.
You’lll find some mildly unflattering things said about this approach, over at Dynamic Ecology. This is a healthful disagreement of opinion. (Heck, there might even be a claim that it wasn’t unflattering!) I recognize that what I’m writing goes against current dogma, that if your work isn’t driven by theory, then it’s not of much value. I can respectfully disagree, but then again, there’s no major concept or principle with my name on it, either, so I can’t push my point too firmly.
If you take a walk through a rainforest, a few hundred curiosities, with no known answers, should slap you in the face very quickly. This happens during a walk during the desert, as well, though with lower frequency as there’s less biomass.
When I walk through the rainforest, I see something new every time I step out. Among the things that visibly move under their own power, ants are clearly the dominant feature of rainforests. If I want to be able to ask a whole bunch of questions, and had to pick a taxon, ants are a good way to go. (A well known and true event is that Bert Hölldobler and Ed Wilson spent two weeks together at what is now my field site; it resulted in three very cool publications based on what they found.) One major unexplored frontier is the leaf litter of tropical rainforests. Nearly all of the the primary production of the forest ends up on this thin layer between the sky and the earth, as Jack Longino once said, and we know so little about it and its denizens. It’s a big linkage in food webs that is a huge black box with respect to most fields of ecology (aside from ecosystem ecology, though this is still not as well known as it could be in this respect).
Now you can see why I have trouble assembling an elevator talk.
I propose a taxonomy of research goals, with three domains:
- Discovery. Finding or creating something brand new – a species, a theory, a mechanism.
- Improving ideas. This is the theoretical bandwagon – amassing evidence to flesh out, support, refute or modify existing theories.
- Tinkering. There’s a little something that doesn’t make sense and you want to figure it out. Your goal is not to create a new theory or to test specific hypotheses.
Obviously the third category wouldn’t sit well with funding agencies. That’s not keeping me from adopting this approach as my primary orientation. From reading my papers, you wouldn’t necessarily be able to tell which primary goal led to a particular manuscript, though it’s almost always the result of tinkering. You can’t sell tinkering to well-read journals in the current environment. They want you start your story as if your experiment was always designed to test one very specific hypothesis, even if everybody knows that isn’t true.
When I’m wondering what project I want to do next, I do a few things. I weigh a bunch of factors – what’s fundable, what’s do-able, and what’s publishable.
Then I notice the file on my desktop, and I toss all of that crap aside.
I do that little thing that’s always been nagging: “Answer me!” Then, I go off and do that project. My only problem is that the list of nagging questions is far too long for me to answer in one lifetime.
You might be asking, “How’s that working out for ya?” I’ll get to that next week with some specific examples.