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

Biodiversity Challenge: Biodiversity hidden in plain view

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

I’m trapped in a barren wasteland. It smells of PineSol and fast food. There are people milling about all around me. They are coming and going in and out of little hallways, and there are so many iphones! Everyone is looking at their iphone! I am at the Dallas Fort Worth International Airport. There’s nothing here. Everything’s so sterile (which I guess is an improvement over the way it used to be). There can’t possibly be biodiversity here.

photo (2)

But wait! What’s that, over there by the power outlet? That filth! Those crumbs! There! That’s biodiversity! And there’s more! There’s biodiversity all over that bag of chips, and on the drinking fountain handles. There’s biodiversity on all of those iphones!. And there’s biodiversity on all of the people. All of them are teeming with germs! PineSol, you don’t stand a chance. There’s so much diversity, and it should stay that way!

Traditionally, when people think about biodiversity, they focus on the things that they can see: Tropical rainforests, African savannahs, wildflower meadows, even diversified agriculture systems. For me, it started with mangrove forests and grasslands, but recently, I’ve become more and more interested in the biodiversity that’s all around us that you can’t see. And I’m not the only one thinking about biodiversity hidden in plain view. Researchers are studying biodiversity in our houses, on our bodies, in hospital air, even inside the leaves of plants!

And those researchers are finding incredible things! The microscopic creatures inhabiting houses with dogs differ from houses without dogs, and might even contribute to healthier people in those houses. The microbes on our bodies vary by who we are, where we look, and even how much roller-derby we play.

Ok, Fletcher, so there’s biodiversity all around us, and some of it is pretty cool. But why on earth would you recommend that we conserve biodiversity in an airport? You’re talking about germs! People get sick in airports!

Well, although there’s a lot that we don’t know about the hidden biodiversity around us, we do know a few things. There are microscopic bacteria and fungi everywhere. And they’re important. We know that some of them cause diseases, but it looks like some of them might protect us from diseases, too.  We know that they can interact with each other, that they can form communities, and that those communities can be really different from each other. And I’m not talking apples and oranges different. I’m talking sea cucumber and redwood tree different, all in one square inch! And for the most part, we don’t know how they came to be different, but when we eliminate these communities from the face of the earth with PineSol or antibiotics, the communities that replace them are unlike those that were there before.

So we should conserve biodiversity at the airport because we don’t understand it. We should conserve biodiversity at the airport because it might just protect us from some of the diseases that we’re trying to prevent**. We should conserve biodiversity in the airport for the same reasons that we should conserve biodiversity in the Amazon and in the oceans and in our backyards. We should conserve it because it’s there.

30 October, 2013

*I should confess. I don’t study the microbial ecology of airports. I know virtually nothing about them other than what I’ve inferred from the references above.

**Alright, that might be a bit of a stretch. I am an advocate of sanitation at airports

Tradeoffs, correlated traits, and functional diversity

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

Tradeoffs are everywhere, and never has this been more apparent to me, than in graduate school. With only so many hours in a day, and an ever-growing to-do list, how I choose to allocate my time becomes an increasingly important decision. Do I work in the greenhouse, resample my field experiment, analyze data, catch up on reading…? Every day, when I wake up, I’m faced with these decisions.  And every day, these decisions are constrained by the same two major factors: What can I do? e.g., how much time do I have in the day; and what have I already done?

Well, I’m glad to say that I know I’m not alone. In fact, most organisms face nearly the exact same constraints. And these two constraints don’t just occur within a single organism’s lifetime. They can often be reflected over evolutionary time, too. In this case, “what can I do?” becomes a question of physiological constraints on phenotypes (some combinations of traits are physiologically impossible), and “what have I done?” becomes a question of evolutionary history, or natural selection (some combinations of traits would confer fitness disadvantages).

As studies of diversity move from descriptions of species numbers (e.g., taxonomic diversity) to descriptions of species physiology (e.g., functional diversity) or evolutionary history (e.g., phylogenetic diversity), it’s becoming more important that we pay attention to the tradeoffs that underlie those patterns. Although not the first to suggest this, Wright et. al’s description of the worldwide leaf economics spectrum demonstrated the universality of tradeoffs between natural selection and physiological constraints, and argued that plants tend to fall on a continuum between two fundamental strategies for dealing with these tradeoffs, termed the slow- to quick-return continuum.

This spectrum runs from species with potential for quick returns on investments of nutrients and dry mass in leaves to species with a slower potential rate of return. At the quick-return end are species with high leaf nutrient concentrations, high rates of photosynthesis and respiration, short leaf lifetimes and low dry-mass investment per leaf area. At the slow-return end are species with long leaf lifetimes, expensive high-LMA leaf construction, low nutrient concentrations, and low rates of photosynthesis and respiration.

For example, imagine you are a small grass seedling, your goal in life is reproduction, and you only have a finite number of resources to allocate in order to reach that goal. Do you allocate them to growth and additional resource acquisition, or do you conserve the resources that you have so that you can allocate them all to reproduction? What Wright et al. suggest is that you are fundamentally asking, “Should I be a quick-return plant or a slow return plant?” Physiologically, it is not possible to exhibit both high rates of photosynthesis (future resource acquisition) as well as low leaf nitrogen concentrations and long lived leaves (resource conservation). In addition, if you choose to allocate few resources to photosynthesis, jack up your leaf nitrogen concentrations, and rapidly shed leaves, you are unlikely to successfully reproduce. As a result, your phenotype is constrained physiologically and evolutionarily, and Wright et al. argue that this tradeoff is fundamental across all plants and results in a predictable spectrum of phenotypes.

I was introduced to this paper very early in my graduate career, long before I had a flicker of an inkling of a speck of a thought about the multiple dimensions of biodiversity. But when I start to think about patterns of functional diversity through the lens of the leaf economics spectrum, I start to wonder. If groups of physiological traits covary and are constrained by physiological processes and evolutionary history, how might this influence the inferences that we draw from patterns of functional diversity? When measuring functional diversity, how important are the specific traits that we consider? And if groups of physiological traits are strongly correlated along a phylogeny, how useful are measures of phylogenetic diversity at inferring patterns of functional diversity?

Is blogging effective at communicating biodiversity research?

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

My original intent in writing this post was to compare the 5 most-cited papers on biodiversity to the 5 most blogged-about papers on biodiversity to address the differences between what we value as researchers versus what we value as general science communicators. However, I was shocked by the results of my search.  Over 49,000 papers have been published containing the word “biodiversity”.  In contrast, only 448 blog entries on researchblogging.org contain the word “biodiversity”, citing just 427 papers. What does this mean about the state of biodiversity research versus the state of biodiversity-research communication? Do bloggers and their readers value fundamentally different research than that being conducted and cited? Or are researchers simply falling short of effectively communicating the most important research in biodiversity science? Here at biodiverse perspectives, we aim to bridge the gap between research blogging and scientific research, by focusing on the research that we consider to be truly transformative in the field of biodiversity regardless of publication date.


In this blog, we present the papers that we think are the foundational and frontier papers in biodiversity science. But we are just a subset of a vast scientific community. I recently began to wonder, if I were able to poll all biodiversity researchers, what would they say are the five most important papers for biodiversity science?

Well, I don’t have the eyes and ears of all biodiversity researchers, but I do have some tools for garnering their opinions. If journals are the primary method for sharing scientific material, then to some extent, the number of citations should tell us something about how we value research.

So, I sent a letter to every published biodiversity researcher:

 Dear ISI Web of Science,

What are the five most-cited papers that contain the word “biodiversity”?


Fletcher Halliday

And, believe it or not, I got a reply! Here’s a list of the top five cited articles from Web of Science:

Myers et al. (2000) Biodiversity hotspots for conservation priorities. Nature. 4,790 citations

Vitousek et al. (1997) Human domination of Earth’s ecosystems. Science. 2,410 citations

Sala et al. (2000) Biodiversity – Global biodiversity scenarios for the year 2100. Science. 1,764 citation

Thomas et a.l (2004) Extinction risk from climate change. Nature. 1,690 citations

Hewitt, GM (1996) Some genetic consequences of ice ages, and their role in divergence and speciation. Biological Journal of the Linnean Society. 1,667 citations

But this website wasn’t designed just to be a compendium of articles that may or may-not be well cited in the literature. As the name suggests, the purpose of this website is to present the perspectives of a diverse community of graduate students. In many ways, this blog is unique. We have over 15 contributing authors, representing 5 countries, and we focus primarily on sharing our opinions on primary literature in biodiversity science. However, in many ways we aren’t so unique. In fact, there are over 2,500 blogs on the web registered as “research blogs” with the website researchblogging.org. And it seems to me that my letter to every published biodiversity researcher may have missed a large segment of the scientific community.

So I sent out another letter:

Dear Researchblogging.org,

What are the 5 most blogged-about papers containing the word “biodiversity”?


Fletcher Halliday

And researchblogging.org replied too- and what a surprising reply it was! Of 448 blog posts, only 19 papers were written about more than once and only 2 papers were written about more than twice:

Evans, et al. (2011) The spatial distribution of threats to species in Australia. BioScience. 3 blog posts

Strassburg et al. (2010) Global congruence of carbon storage and biodiversity in terrestrial ecosystems. Conservation Letters. 3 blog posts

17 papers tied for the remaining three slots in the top 5, each with 2 posts apiece. They ranged in subject from the use of DNA barcoding to infer patterns of avian diversification all the way to role of the Chicxulub Asteroid in mass extinctions.

I wasn’t surprised that the top-five papers were different between ISI and researchblogging.org, but I was surprised to find that the top-five most-cited articles on ISI have never been written about on researchblogging.org. What does it mean that the 5 most important papers to biodiversity researchers don’t even register with biodiversity bloggers?

I’ll pose 3 possible explanations and then leave it up to you to decide what we need to do.

First, perhaps researchblogging.org isn’t a representative sample of science blogs on the web.  But then, if researchblogging.org is not, then what is? If blogs about research aren’t easy to find, then are they really doing their job?

Second, by focusing on very recently published articles, researchbloggers are missing some of the more foundational research in the field. Researchblogging.org launched in 2008 and consequently, the vast majority of papers that have been blogged about were published after that time. Maybe the purpose of researchblogging isn’t to share the most important research, but rather the new and exciting research. However, by only focusing on recent publications, do we run the risk of perpetuating the trend in ecology to reinvent the wheel?

Finally, perhaps not enough researchers are contributing to researchblogging. There are WAY more publications than there are blogs about them! In fact, ISI gave me more than 49,000 results for my query of papers using the word “biodiversity”, whereas researchblogging.org gave me 448 blog entries, citing 427 papers. Just to put this in perspective, the most cited paper containing the word “biodiversity” has been cited 10 times more than the total number of blogs on researchblogging.org that contain the word “biodiversity”. Maybe research blogging and the literature don’t agree because not enough scientists write in blogs.

If science blogging is intended to disseminate science to the public, then it seems important that science blogs aren’t limited to presenting just the newest and most exciting research out there. Here at Biodiverse Perspectives, we are trying to put biodiversity research into some kind of context by writing about papers that are new and exciting as well as papers that have contributed to our foundational knowledge of the field. We hope that this endeavor will allow us to share our excitement about the future direction of biodiversity research in light of its past. What do you think?