Diverse Introspectives with Tony Ives

This post was originally published on BioDiverse Perspectives – a research blog aimed at fostering communication about biodiversity.

On October 29, 2013, graduate students Rob Heckman, Claire Fieseler, and I sat down with Dr. Tony Ives, Plaenert-Bascom Professor of Zoology at the University of Wisconsin–Madison. Dr. Ives may be best known for developing theoretical models to explain complex population dynamics in lake midges and predator-prey dynamics of pea aphids and their parasitoids, but his research interests are broad. He has published over 120 articles on a huge variety of topics in population and community ecology from coexistence in carrion fly communities to phylogenetic methodology. He has won many awards and honors for his research, most notably the 2012 Robert H. MacArthur award from the Ecological Society of America for his work on population dynamics of midges in Myvatn, Iceland. Dr. Ives was elected to the American Academy of Arts and Sciences in April 2013. We were fortunate to sit down with Dr. Ives when he visited the University of North Carolina for the distinguished lecture in Ecology.

Midges swarm over Lake Myvatn, Iceland. Photo taken by Arni Einarsson
Midges swarm over Lake Myvatn, Iceland. Photo taken by Arni Einarsson

Congratulations on your recent MacArthur award. What was it like to win such a prestigious award from your peers?

It was a huge honor, especially because it was from my peers. But honestly, it was very much a joint award. It was the result of the work of a lot of people. I’ve been incredibly lucky to get great scientists through the lab, and it is really them who deserve the award as much as me.

In the lecture, you started with a question about whether ecology should be about general laws. Why did you feel that it was important to begin your lecture with such a provocative question?

To get people thinking. Most of my talk was about midges in a weird lake, in a weird place – Iceland. How do I justify working on such a peculiar system? How do I justify this in a broader context? Ecologists often try to work only on problems that are inherently broad and apply to a lot of different systems. I couldn’t justify our weird study in this weird lake on those grounds. So I needed to start with a justification for working on something that’s strange, but nonetheless can give broad answers or conceptual understanding.

The midges of Myvatn. Photo taken by Arni Einarsson
The midges of Myvatn. Photo taken by Arni Einarsson

On the issue of universal laws: I don’t think there’s anything universally true about what you’d find in a particular lake. It’s the differences among lakes that I think are interesting. As a theoretical ecologist, you might think that I’m motivated by general laws. But I don’t find general laws very interesting. I really like solving problems. If I’m using theory and not looking for universal patterns or universal laws, then people ask what the hell am I doing? My answer is that I think of ecology as a library of well-developed case studies. If you’ve come across something in your own system, you can go to the bookshelf, pull out a book – a case study – and read it. And maybe there’s some insight that inspires you to look at your system differently. This makes case studies very useful for ecology.

I wouldn’t argue that all case studies are singular and have nothing to do with each other. Clearly there are a lot of themes that cut across different systems. But I wouldn’t necessarily uphold them as laws that you’d expect to see in every system.

If you think about ecology as a collection of case studies, then theory aimed at problem solving fits in as a type of case study. You can take a model and analyze it to death. What’s nice about a model is that you know absolutely everything about it. That’s not like any ecological system, where there’s always going to be stuff that you don’t know. A model is very well defined — you can analyze it and really understand it. The model then becomes a case study — a book on the ecological bookshelf. If you’re looking at your new ecological system – your real system – and you find something that doesn’t make sense, then you can look back at a model, and maybe it will spur intuition about your system. Using models as case studies puts theory on par with empirical studies. I think conceptually, intellectually, logically, they are on par, if you think about them as providing inspiration.

To give an example, I like to use Bob Paine’s work on Tatoosh island. Bob Paine’s classic studies in the 60’s defined keystone species. This is a broad concept that people find very, very useful across a whole variety of systems. But think about what Bob did: He studied the intertidal systems on one island, and he collected all the data himself. From a statistical point of view, all of his conclusions about keystone species have to be confined to what goes on in these intertidal communities on Tatoosh Island. Yet, ecologists are quite happy taking the inference from that single study on that single island, and applying the idea of keystone species to a whole variety of ecosystems. That is an incredibly abstract thing to do. I don’t view doing the same thing with theory any more abstract than doing what people are already comfortable doing with Bob Paine’s work.

So, I use theory to try to solve specific problems, to find general laws. That is what is fun for me. But I hope that the specific problems can at least spark ideas for other people studying other systems.

Can you share with us a paper that was particularly influential to you when you were a grad student or early career scientist?

I have to confess that when I was a graduate student, I didn’t like reading “old” papers. But I should have. One of the things that I notice now is that I read ideas in papers that are being published today, and I think ‘Oh gosh, there was a paper that was published in the 70’s that was pretty much the same.’ I’m always amazed at how the memory of science is fairly short. But that’s not answering your question.

Maybe the most interesting paper that I read as a graduate student was Nicholson and Bailey, 1935. I worked on carrion flies as a graduate student. And Nicholson worked on carrion flies. You go back to this paper published in 1935, and all of the basic questions that they were asking were the same as people were asking when I was a graduate student. To a large extent, they are the same questions that people are asking now. On the one hand you could get depressed and ask “Have we really not come very far in the field?” But I think a more sensible interpretation is that Nicholson and Bailey were asking really good questions that don’t have simple answers, and we’re still asking the same questions. So these are rich questions, and therefore they’re good ecological questions. Nicholson and Bailey got me to recognize that the good questions are hard questions which are not going to be easily answered, at least not in my lifetime.

Do you have recommendations for how grad students or people starting out should read papers?

Oh, I don’t know. I think people should just read what they want to read. And people typically will do that.

I would encourage people to read a lot. I’ve gotten unbelievably bad at reading. I do batch reading, so if I need to know stuff for a particular project, I’ll just download 200 citations and read all of the abstracts, and from that pick papers that I want to read. But that’s not a very good way of keeping up with the broader literature. So I wouldn’t recommend doing what I do.

When I was a grad student, I was pretty good at reading broadly. I had a key to the library, and every Sunday morning I would go into the library – it actually used to be Robert MacArthur’s office, which is cool – and I’d go through whatever journals had popped up on the shelves in the last week. I’d read anything that had an interesting title. I guess now, nobody reads paper journals anymore, but there are easier ways to see what’s being published. I’d recommend people keep their reading broad.

Are there particular skills that you wish you had cultivated in graduate school? How do you think they differ from skills that scientists should be especially keen to cultivate now?

I think that’s the wrong question. I don’t think graduate school should be about cultivating skills. This makes it sound as if your brain ossifies when you get your PhD and you can’t learn anything after that. For me, I learned almost everything that I know about statistics after finishing a PhD. So, rather than cultivate skills, I would say you should come up with questions that you’re interested in and then learn the skills that you need to answer the questions. It has to be question driven skill development. I get students coming into my office sometimes, saying, ‘I want to do more theory in my work. What kind of theory do I need to know?’ And I say, ‘Come back when you have a biological question, and then we can talk about it.’ I think the biology should drive things, not skill development.

If you could go back in time and tell a graduate student version of yourself one thing, what would it be? And is that different than the advice that you would give a grad student now?

The year I entered grad school, I think there were two ecology faculty positions that opened up in the entire country. It was early-mid 80’s, there was an economic slump, and things were bad. I dealt with that by telling myself, I’m going to be in grad school not as a means to an end. I decided to stay in grad school because I couldn’t think of anything else that I wanted to do more. I couldn’t help myself. So, I stayed in grad school, and by the time I finished, jobs had opened up.

I guess my advice would be to live for the now, to study what you want to study, to be comfortable in what you are doing at this moment. Don’t try to do science by making sacrifices now for something that you expect in the future. If you make sacrifices now in a way that you think could help in the future, there’s no guarantee you will be right. Much better to simply do what you want to do now, because that’s going to make you more successful in whatever you do, and that’s going to lead to success however you measure success in the future.

Success in graduate school, at least of the grad students I’ve seen, comes from finding out pretty quickly what you’re good at and then pursuing it. Allowing yourself to be engrossed by it. Ultimately, that’s going to make you the most successful, whether that involves  teaching, whether it means working on very applied problems, or whether it means doing very, very basic research. People who are most successful seem to be those who figure out what they really enjoy doing and then just do it.

Can you tell us about a particularly memorable experience that you had doing fieldwork?

Well, okay, maybe I shouldn’t tell this, but it is the story that popped to mind most quickly. I discovered that I have a very difficult time doing research that involves simply sitting and watching something. I need to be doing something. I tried to do an experiment that involved sitting, watching carrion flies coming to dead carcasses. It was just unbelievably boring. I’d been doing it for a few afternoons, and I thought maybe it would be a nicer experience if I took a few beers with me. I finished the first beer, maybe 2, and after about an hour of sitting and watching, I thought, well, it’s a nice afternoon, maybe I should just like lie down for a little bit. I woke up at sunset. I concluded that, no, you should not mix alcohol with field work, and also that I should give up watching carrion flies at carcasses. So I did both.

Are there any other epic failures that have been important to your career?

I have had some epic failures that have just simply been epic failures, that have not led to anything good. One of the things that I’ve learned is to allow myself to be epically wrong. My graduate students will testify to that. I’ve said some things in lab meetings that made other lab members ask whether it is possible for me to say something sufficiently stupid to have my PhD revoked. But I think to be a good scientist, you have to be prepared to be wrong, and wrong in not a  ‘Oh I was wrong but I learned so much that good came out of it’ way, but just good plain wrong.

The freedom to be wrong is important. I’m probably more wrong than anybody else in the lab, and I think people need to know that, because you can’t live life as a scientist always being scared of being wrong or failing. It’s going to happen, and you have to get comfortable with it.

It seems like you’ve done a great job of overcoming your own imposter syndrome and setting a stage to help prevent it in your lab.

Honestly, sometimes I still have the oh-my-god-how-am-I-going-to-find-a-job nightmare. Okay, maybe its only once or twice a year now, and when I wake up I do have a job. Actually, I have tenure — cool. But I still have an imposter syndrome. I certainly did with the McArthur award. I don’t think I’ll ever get over the imposter syndrome. I’d like to say that it doesn’t affect me — that it doesn’t mean that I intentionally avoid things. But it does, and I do. I don’t think I can change that, though, and I don’t really want to.

What opportunities in your career have been most unexpectedly valuable? Are there any opportunities you wish you had taken?

I don’t know whether this answers the question, but a lot of the work that I do is collaborative. And I have stumbled into collaborations in all kinds of strange ways. I stumbled into the project in Iceland simply because I had family connections in Iceland. I wanted an excuse to go see family friends, and so for the first and only time in my life, I invited myself to give a talk at the University of Iceland. That turned into a 15-year collaboration with Árni Einarsson. Most of the fun collaborations that I’ve had were stumbled into. But this has lead to meeting great friends and colleagues and scientists. This has really been one of the most fun things about my job.

Midges darken the sky over Lake Myvatn, Iceland. Photo taken by Arni Einarsson.
Midges darken the sky over Lake Myvatn, Iceland. Photo taken by Arni Einarsson.

When does stumbling on an interesting opportunity become a good collaboration, specifically for the work that you’re doing in Iceland?

One of the most important things about a collaboration is enjoying the people that you are collaborating with. Sometimes there’s a bit of a dating process as the collaboration evolves. I would never underestimate the importance of getting along with people.

For example, Árni Einarsson is an incredibly nice person who I get along with very well. He is also an unbelievable naturalist. At the beginning of the season in Iceland, he’s doing the bird count at Lake Myvatn, and I always try and go along with him. Just walking through the landscape of Iceland, where he’s at home, is magical. He has all kinds of stories: ecological stories and archaeological stories. It’s really fun. Having nice and interesting collaborators makes the collaboration work. Collaborations have to do with science, but they’re also very personal.

What do you think is the appropriate balance between empiricism and theory given the renewed interest in the role of the two in ecology?

Oh, that’s easy. It’s whatever you want. There are some people who think in numbers, and there are some people who don’t. It’s totally individualistic. I don’t think there’s a blanket answer to your question. I think people should do what they want to do and if that involves theory, fine, and if it doesn’t, that’s fine too.

Is there anything else you’d like to share?

Just a reiteration that I think to be successful, the best strategy is simply deciding what you like to do. If you like to do it, you’re probably good at it, so you should just do it. That’s probably the best ticket to success.


11 March 2014

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