Ant science: how avoiding modeling led to a cool discovery

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Here’s a specific example, from my own work, of how the avoidance of mathematical modeling led to a fundamental discovery that eluded modelers and experimentalist for decades.

At least, that’s how I see it when I’m not feeling humble. It’s about resource allocation in ants, not the grand unified theory, after all.

For context, for those newer to the site, consider this post as a coda to an ongoing series (and discussion of sorts with Dynamic Ecology) about approaches to designing a research program. I have advocated that exploration by tinkering with unexplained curiosities within natural systems often leads to the best discoveries as well as the most consequential research programs. This post from a few weeks ago provides a good summary of that series. Another precursor to this post is a discussion about the relationship between mathematical modeling, hypothesis development, and how much math you need to become a scientist.  That is also a precursor to this post, though it is a “long read,” for those averse to verbiage.

The subject of this post — the scientific discovery — came out in a paper last year (go read it if you wish), which I wrote with Sarah Diamond and Rob Dunn. In short, we discovered a fundamental pattern that could have been obvious to everyone, if anybody just looked in that direction. This pattern explains many unanswered ideas, going back to theories that E.O Wilson developed in the 1970s, along with George Oster.

A twig nest of Pheidole sensitiva. Photo: Benoit Guénard

A twig nest of Pheidole sensitiva.
Photo: Benoit Guénard

Oster & Wilson set out to understand what regulates the varying levels of investment into the different members of ant colonies. Most inhabitants of ant colonies are functionally sterile, and in some species, there are multiple physical castes of sterile ants.

The genus Pheidole is the most species rich ant genus, and they’re found pretty much everywhere. All Pheidole (aside from a few exceptions) do something that isn’t found in many other lineages: they have two discrete sterile worker casts. They make big-headed soldiers and tinier minor workers, both of which do a variety of work for the colony. Some think that this dimorphic worker caste, and potentially the flexibility tied to its production, has enabled these ants to not only become ecologically successful but also to diversify.

Anyhow, Oster & Wilson made a number of predictions about the adapability of the ratio of soldiers to minor workers in Phediole colonies. One of their big testable predictions, or perhaps it could be seen as model to be falsified, is that the colonies actively adjust the ratio of soldiers to workers in response to environmental challenges.

It entirely makes sense. If a Pheidole colony is in an environment that requires more soliders, they would make more soldiers. Right? The problem is, despite a lot of looking carefully at Pheidole colonies, this wasn’t found. Finally in the mid ’90s it was found in the lab of Luc Passera, that P. pallidula colonies made more soldiers when they were exposed, without contact, to neighboring colonies. When I say it was found in the lab of Passera, I mean it happened physically in his lab. These were captive colonies.

A similar thing was found in the field in 2002, when I and Jeb Owen published a paper showing adaptive soldier production in another Pheidole species. (Also, my labmate Samantha Messier did the same thing before the Passera group, in a field experiment involving Nasutitermes termites and a machete.) Our studies were done in the field. In my experiment, when I put clumps of supplemental food in the field for months on end, the food was defended by soldiers, and in a short time colonies made more soldiers.

One thing I didn’t mention at the time, though, was that I didn’t find adaptive soldier production in a whole bunch of other species. However, I had less statistical power, and it was the most common species that showed this pattern. Maybe the less common ones did, but it was harder to detect.

If you were to ask around and dig into the literature, you’d see that it’s pretty clear that most species of Pheidole actually do not overtly shift their caste ratios when you mess around with their environment. Not every colony produces the same ratio, but a systemic environmental manipulation doesn’t cause an increase. Other than the two papers I just mentioned, I don’t think anybody else has found adaptive caste ratios in Pheidole. Others have looked, but it hasn’t emerged very clearly.

So, if most species just don’t ramp up and ramp down soldier production in response to the environment, what controls soldier production? For decades, there has been a consistent amount of work asking this question from behavioral, physiological and developmental angles. In the course of all of this excellent work (a lot of it being done by Diana Wheeler, Fred Nijhout, and their associates), we’ve made a lot of progress in understanding how colonies regulate their activity and how development is regulated through genetic, biochemical and physiological mechanisms.

One thing that I’ve always wondered about is, why do some species produce more soldiers than others? I’ve cracked open lots of twigs, and the numbers of soldiers are highly variable. And my experiments have shown that most species don’t obviously change their soldier production in response to environmental changes. There has been lots of great work to understand variation within a single species, but interspecific comparisons have been scant.

I can understand why there hasn’t been much comparative work. Measuring caste ratios of entire colonies can be hard. Find a Pheidole colony in the back yard and compare the number of soldiers and workers. See, not easy, huh? You’ve got to dig them up. Unless, of course, your backyard is a rainforest. In that case, you just pick up twigs. Over the years, I estimate that I and my students have picked up over 106 twigs over the years. Thousands of these have had Pheidole colonies inside. The rainforest is diverse, so I have data on many species. How do they compare?

Well, I learned that the caste ratios were different among species. Some species produced way more soldiers than others. Considering that we know so little about the natural history of these species, there wasn’t a great basis for comparing many of these species to one another. But one thing we could examine, quite easily, was body size. And, as it turned out, that was super-duper predictive of solider investment. Smaller species produced more soldiers than larger ones. When this pattern emerged on my laptop, it was one of those moments of elation that are very cool, but then you don’t have anybody with whom to share.

Then, I dug through the literature so see if the information that we had about caste ratios and body size shows the same pattern that I found in my rainforest. It turns out that the relationship is as identical as you can get. Our local scale pattern recapitulated Pheidole from around the world, and across the phylogeny.

Now, if you ask someone, what controls soldier production in Pheidole? You can say the answer is quite clearly body size. How and why does body size control this? There is some cool work that’s been done on this intraspecifically, that presumably is a mechanism that works more broadly.

How did my discovery of this generalized relationship come about from avoiding models? If you look at the work on soldier production, ever since Oster & Wilson published their monograph in the 1970s, there’s been a strong emphasis on modeling the mechanisms that trigger and regulate soldier production. Meanwhile, nobody before me bothered to step back to look at the big picture and ask, “how are species different and what is predictive of that?” If they did, then they would have found the caste ratio data in the literature as I had, and looked at the most obvious predictor: body size. Others were modeling solider production. I was merely trying to find a pattern.

I’m not claiming that the discovery of this pattern is earthshaking or that it explains mechanistically how colonies make more or fewer soldiers at the proximate level. The main take-home message from this paper is that many of the differences we find are driven by constraints rather than by adaptation, or that selection on body size is coupled with selection on soldier production. This leads to a lot of exciting thoughts about community structure, which we’re now working on.

This work by no means diminishes all of the careful experiments that others have done over the years on Pheidole. Though I’m not a developmental biologist nor as much of a behaviorist, I was able to find something that will be (or at least, I think should be) at the basis of future conversations about the evolution of caste ants.

This is why my choice is to keep asking “What is the pattern?” rather than attempting to model patterns.

How tinkering can work as a research program

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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.

Tinkering around is the best way to do research

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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.)

Darwin was a tinkerer. (Richmond's portrait of Darwin is from 1840)

Darwin was a tinkerer. (Richmond’s portrait of Darwin is from 1840)

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.

Tinkering.

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.