This is the fourth and final post in a series, wherein I attempt to make the case that tinkering is a viable, and perhaps optimal, approach to conducting a research program, particularly for those at teaching-centered institutions. Here are the first, second, and third posts preceding the present post.
I’m a tinkerer. That means that I don’t typically design my research to fit the framework of a big theory, but instead I set out to answer a small little question that has occurred to me. I do experimental research, combined with observational research, to find the answers to open questions. I’m just not going after the big fish that other labs do. After all, I work in a small pond.
This is a personal narrative about how tinkering has worked for me. It’s hard to write about the concept in the abstract, so I’m going into the specifics about one line of tinkering I’ve done over the years. If I am going to make the case that tinkering works well for me, it’s easiest for me to to use specific projects to illustrate how tinkering has worked for me. So if you read on, you’ll be reading about ants. Consider yourself forewarned.
When I started as full-time faculty at a teaching institution, I found myself with the position of having a field season in front of me. What did I want to do?
I quickly decided that I wouldn’t continue along the lines of my dissertation, which was on the biology of invasive ants. There were so many questions about biological invasions that were interesting to me, but they all seemed too, well, big. For all of the specific big questions about invasiveness that I wanted to tackle, there were other labs that were going at it at the same time, full time with multiple collaborators, without teaching. (In the end, their work was — and still is — awesome in its creativity and quality, going well beyond my initial interests. In my position, I don’t think I ever could have run most of the experiments they have, at least not on the scale that they did. I admire their work a lot.)
My dissertation was one part of getting the invasive ant bandwagon rolling, but after taking a job at a teaching institution, I needed to find a better ride. I had a few papers that made a difference, by looking at the issue from a broader-than-usual perspective, and it was time to move on.
I knew that I wanted to get back to my field station in Costa Rica. It was a place that I knew well from my dissertation, and it had become kind of a second home to me, and I hadn’t been down there for 18 months. I had a few weeks on site, along with several undergraduate field assistants.
I wanted to pick a project that fit three criteria:
- The project could be completed in a few weeks
- The project lead to a modest publication, regardless of what the results were
- It would be fun
Here was my thought process: This rainforest is chock-full of ants, everywhere. People study them all of the time. But they only study the cool and bizarre ones, like leafcutters, bullet ants, ant-plant mutualists, and army ants. There are hundreds of ants that make the forest run that are overlooked. I wanted to study one of those. So, I picked what I thought what was one of the most common, but unknown, species, and designed a cute little project around it. (By the way, free versions of all the papers in this post are found on my website.)
My main goal was to ask, “What is up with this extremely common species that we know nothing about?” I built it around a question about unpredictable resource heterogeneity, competition, and whatnot, but it was mostly a vehicle to play around, because I knew nothing about this species. And I wasn’t going to go down for a few weeks and not get a paper out of it.
Even though I designed that cute little project to be fail-proof (negative results would still be publishable), I barely eeked that paper out. That was because my sample size was dropping precipitously throughout the short experiment. We started out by marking a bunch of colonies in the field. As days progressed, the colonies flat out disappeared. Their nests were just empty holes. By the end of our experiment, we sorted out that they just moved nextdoor. Over the course of a few weeks, we’d lost well more than half of our colonies, but I didn’t have data on them after they moved.
The next field season — one year later, after my first year on the tenure track — I had a few more weeks with a team of undergrads. I wanted to understand the non-optimality of home range size. I was ready for nest movements, and built it into the experimental design. The answer was kind of interesting: foragers spent more time looking for food before giving up when the home range is of poor quality.
At this point, for two years on the tenure-track teaching a full courseload of new courses, I’ve gotten two okay papers out from two short field projects, while spending time on other projects as well. At the rate of a paper a year, I would’ve been well exceeding scholarly expectations at my university, as a decent first-authored paper per year is pretty good at a teaching institution with a heavy teaching load. I was okay with my publication rate, but I felt like I wasn’t taking this anywhere interesting.
I felt that I knew this critter pretty well. The most curious thing was nest movement behavior. Delving into the literature on nest movements in ants, I found that nest movements have been documented aplenty. But in each species, it was studied only once. It looked like everyone experienced what I did – they stumbled on the phenomenon which botched an experiment, and then they wrote up how the experiment was botched by nest movements. Then, they moved onto more tractable systems, using animals that don’t disappear when you’re not looking. Nobody had gotten far beyond the nest-movements-botched-my-study study.
I decided to directly tackle nest movements in my next field season, which was, again, with several undergrads for about a month. All I wanted to know was, “why do they move their nests all the time?” You can’t ask “why” questions with science, though, so I asked “how” and “with what consequences, correlates and a potential cause.” These results were really interesting to me. It turns out that they move, on average, about once per week, and it has nothing to do with food or competition.
After working on a variety of other things, I wanted to take some time to get back to these mysterious nest-moving ants. My earlier work suggested – only vaguely – that odors might play a role in how they move their nests. I wanted to see if this was the case. So, I ran an experiment by experimentally manipulating nest odors. It turns out that nest odors can keep them from occupying or staying in nests, but the manipulation had enough artifacts I can’t really trust that this experiment explained what was really happening.
While working on other stuff, this nest odor problem kept nagging at me. Eventually, while I had students doing a variety of other things, I cooked up a field manipulation for myself to run, by reducing odors within the nest. That made them like their nests more than they would otherwise. But then, again, what does this really show? If their endogenous odors make them dislike their nests, what’s the selective pressure behind nest movement? That’s a really hard question to address.
That was a few years ago. I’ve just returned to it last year. With one student student, I have (meaning, she has) rerun the earlier odor manipulation, but with narrow chemical fractions to identify which compounds are playing a role. We also have additional observational work happening to test some newer hypotheses. These projects are involving a chemical ecologist who I brought into this project, as I lack any of that mojo, as well as the equipment. (Sometimes not having the equipment is a good thing, I’ve already argued.)
All of these studies essentially have been a set of little side projects, that in all have amounted to a substantial line of investigation over the years. We know more about the ecology of nest relocation in this species, than any other. By the way, their name is Aphaenogaster araneoides. I eventually worked up a new official common name, “gypsy ant.” (That was Anna Himler’s idea.)
How were those experiments tinkering? Well, one thing you may or may not have noticed is that the only reason I did these experiments was to figure out what’s going on with these ants. I was curious about what they were doing, and so I tried to sort it out. I didn’t come in to working with this system with a big question about optimal foraging, neighborhood competition, or social organization in mind. I just wanted to know exactly what this one species was doing, because it was a mystery to me.
Because I was open to this species to telling me what it wanted to, I let it take me in the direction where I was led. You’re moving your nests all the time? Sure, I’ll try to figure that out. I wasn’t setting out to use nest relocation to evaluate any grand theory about social insect behavior or movement theory in ecology. I just wanted to know about what was causing them to move their nests.
In the process, I documented in some detail how they maintain multiple unoccupied nests, but only use one at a time. This was seen in a few other species, but it was a distinct and heretofore undescribed pattern of nesting. I thought to give it a new name — “serial monodomy” — which might stick. What else do you do when you find something that happens that doesn’t have a name?
This project has gotten me to think more about nest relocation in ants. It’s permeated a lot of my thinking about the biology of this community of ants, and has seeped over into my community-level work. I realized that nest relocation is biologically significant, and is not taken into account in so many studies. And we pick our study systems by focusing on the tractable species: those that don’t move. Looking at what is known, I found that most species are apparently mobile, and those are the ones that we don’t study for this reason. Our whole understanding about ants is very biased. I decided to write a review about that idea.
Ultimately, I think my work on nest movements on ants has had some influence on how our research community thinks about ant ecology. At least there’s been some movement (yes, that’s a pun) in that direction. Not too long ago, the prevailing notion was that typical ant colonies are like plants, that just don’t move. There are some oddballs, like invasive species and army ants, that move around, but everyone else is anchored down.
I’m pointing out to others that this notion is false. I’ve only done work addressing nest relocation with this one species, but in the process I’ve called attention to all of those other species that have been found to do similar things but are overlooked.
Of course, anybody who really knows ants easily realizes that nest relocation happens in a bunch of species. But this fact hasn’t been broadly appreciated, nor had it been documented. By working on this phenomenon, in detail, within one species, I was given the perspective that allowed me to make this concept more tangible across the phylogeny.
If you asked me after I finished my dissertation, what are you going to work on? I never would have said, “nest relocation.” I wouldn’t have identified any major concept or theory. I mostly was focused on teaching, after all. I wanted to do some cool projects when I had the chance. This brought me to working with a very common ant, which compelled me to figure out its nest movements because that’s a basic part of its biology. I was just tinkering around with it to figure it out, that’s all. But following that direction, once in a while over the years, I’ve built together a set of substantial ideas, that I imagine will continue to matter for some time to come.
This work on nest relocation on ants isn’t earth-shattering. But it is changing, just a little bit, how we think about ants, including changing some long-held and mistaken assumptions. This is just the result of five trips to the rainforest for 2.5-5 weeks each, over the last 13 years. That’s not too bad.
I think if I went down to the rainforest trying to test a big theory, I would have come back empty handed, or with a few papers that mostly would be collecting dust by now. But simply by wandering off without a specific vision of big theories, I think I’ve done something that results in tangible, if not big, progress.
So, that’s my case for why tinkering is a good way to do science. You might stumble on something amazing, or you might come upon something just mildly curious, but no matter what happens, you’ll learn something genuinely new.
Just imagine what else we’d be learning if other scientists doing basic research, in all kinds of disciplines, started doing research in obscure directions on things that were mysterious to them but didn’t seem of much obvious consequence. I think we’d be learning a lot more about the world and probably develop many new ideas more quickly than we are now.