Diverse Introspectives: A conversation with Bob Paine (14 Comments)


Photo courtesy of Benjamin Drummond for The Natural Histories Project: http://naturalhistoriesproject.org/

On August 23, fellow UW grad students Halley Froehlich, Emily Grason and I had the pleasure of speaking with Dr. Bob Paine, professor emeritus at the University of Washington, for our second installment of Diverse Introspectives.

It seemed fitting for Dr. Paine to be our next interviewee, since he and Peter Kareiva are longtime friends and colleagues who spend much time discussing ecology and conservation over “blood* and bourbon.” We’ve continued many of the themes from that conversation, but you’ll find that Dr. Paine offers a unique and interesting perspective.

From giving birth to such well-known and accepted hypotheses as keystone species and trophic cascades, to mentoring a veritable dynasty of who’s who in modern ecology, Dr. Paine has enjoyed a long, distinguished and influential career which has been recognized by such honors as the Ecological Society of America’s Eminent Ecologist Award, and most recently the International Cosmos Prize for his work in promoting “The Harmonious Coexistence between Nature and Mankind.”

We are so thankful to Dr. Paine for sharing his thoughts and time with us.

*undercooked meat

**Leave your questions and comments below and we’ll be sure they get to Dr. Paine–he’s interested in responding to discussion.**

Congratulations on your recent International Cosmos Prize!

It’s turned out to be more time consuming than expected, not that I’m complaining. I have to give two lectures in Japan in which I’m going to discuss biodiversity as a false religion. All of the recent winners have talked about biodiversity as enumerating species and divining meaning from this. There are a couple of things I want to mention–nature is a better term than biodiversity, and has inspired all sorts of art, culture etc. and then I’m going to give my usual pitch, which is that people experience the world in a local sense. You go to the shore, what do you see: all sorts of flotsam and jetsam, organisms and patterns which interests people. But if you stare out at the vast ocean, you don’t see anything living, basically.

How would you encourage these interests? 

If I could snap my finger and cure the world I would start with small children in Kindergarten. For instance, they love the experience and learn something from  smelling skunk cabbage in the Washington Park Arboretum. They can go to the ocean and enjoy splashing around, but also learn that there is real meaning to that hole in the clam shell. I think it starts with education, and it works.

Is biodiversity still a useful framework?

Have you seen the article that Peter Kareiva and Michelle Marvier wrote that discusses  hotspots and coldspots? It’s a really powerful document. There are lots of places in the world that are characterized by very low diversity but are enormously important in terms of ameliorating climate change, in terms of ecosystem processes that keep our planet livable and they aren’t hotspots. I think one problem with biodiversity is that it has really strict taxonomic limits. Say you want to study birds, someone else snails  and another butterflies. There are maxima for species richness in areas and they are all local and don’t map on one another very conveniently.

When I had just gotten into graduate school–I probably over adored my advisor, he was a wonderful man–we were sitting on his porch in Ann Arbor drinking a beer and he asked me: “Why do you want to travel?” “I want to get out and see things,” I said.  He said, “If you are interested in the variety of life, I can assure you that in the dirt in my front lawn there are probably 60-70 species of micro arthropod that we know nothing about, a rich and mysterious assemblage.” There are old fields around Ann Arbor with thousands of insects, there are still lots of unknowns. When you think about the ocean, and you start looking at fungi, bacteria and viruses, much of the biological world is also unknown.

Continuing with your recollections of graduate school, can you think of a paper that was particularly influential to you at that time?

I was in graduate school when Hairston, Smith and Slobodkin produced their 1960 paper. It was widely discussed in the ecology group at U of M. It was a very interesting take on life. I didn’t pay that much attention to it at the time, but it began to portray the natural world as interactive. And that is a really important point.

I then did a one year post-doc at Scripps Institution of Oceanography where there was a clash between two really wonderful professors. The man I was postdocing with said you have to go out and sample the world and then use all the power of statistics–you sample it, you don’t mess with it, then you mine and crunch the numbers and that describes a static structure of nature. His work is forgotten, because the world changes.

The other man was a physical chemist basically. He said you design equipment to understand the physical process you are interested in, you design equipment to test a hypothesis and need to make a measurement only once. If it doesn’t work, you lost, because you know the equipment is right. If it works, you learn something. He said hypothesis testing and experiments are a vastly more satisfying and fun way of doing science. He was absolutely correct. So that’s what I did when I came here…eventually to the outer coast of Washington and thought “my god this is my playground.” There were lots of things that could be manipulated, there were wonderful patterns, and you could see interactions and you could change the structure of those interactions and in the process learn how nature works.

In comparison to localized experiments, what’s your opinion on the movement toward large observational datasets like NEON?

I think it’s a waste of money. For one, it’s almost entirely terrestrial and avoids shoreline communities. It involves lots of coordinated measurements of the physical world. They all take the same dataset. How is that going to help interpret bird migration or the local crickets, or how would it predict a plague of grasshoppers or whatever? I’m not sure that they have any hypotheses that they are testing. If they are then those hypotheses are fairly invisible or badly formed. So they develop the infrastructure before they develop meaningful hypotheses. This is the trap and way of looking at things that people who study ecosystems fall into again and again. It started out with the International Biological Program which was an expensive disaster. We learn almost nothing from ecosystem programs when we study large entities. The focus might be energy flux, production or the amount of carbon produced per square meter per year etc.– there isn’t much biology there and there is very little room for top down effects.

What unanswered questions would you like to answer or hope that our generation answers?

There’s two or three. I’m trying to find out how the world works, which is a small piece of the problem. I think there has to be concerted effort to slow human population growth because we clearly dominate the organic world and destroy it in the process. Basically globalization–you can’t blame Bangladesh for wanting to be like us, so there has to be some universal amelioration of poverty. At the same time our world is going to have to deal with climate change. If there is a foot or two of sea level rise or ocean acidification, that will be a disaster. By 2100 it will doom all the small Pacific island nations, Florida, New York City, London–you can go around and point your fingers at some of the world’s major ports. The melting of glaciers will have a huge impact. Going back to the issue of education though, we need to educate the politicians.

Do you think it’s a responsibility of scientists to make their science relevant and to communicate it to the public and politicians?

I think scientists have. I think we have to get out and find audiences. There should be a happy balance because it can chip away at the amount of science you can do. But if one has a message which is relevant to the public and believes the public can understand it, there is an obligation to share. You could work with the National Research Council, for instance, I’ve done a lot of that.

What’s your advice to people that want to be advocates and engage and be influential? It doesn’t seem easy.

I think it’s nearly an impossible task. If you want to speak with some authority, you have to have some credentials. The topic has to be relevant in some way. On top of that, there are some people who are very good advocates in a general sense at communicating the meaning of their work. On the other hand, you don’t want a self-promoter because they will just be dismissed. Credentials matter, the message has to be clear. We have to be willing to say “I don’t know.”

People don’t always want to hear the “I don’t knows.” It seems like they want black and white.

Well, that’s true especially of the press. But I think it helps to say: here are some alternatives of causal mechanisms and consequences. For instance, there’s a lot of chaos and uncertainty in the world.

Here we have El Ninos. There was a big one from 1982-84. I was on Tatoosh in July 1984, the lowest tide of the year. We had 15 inches of rain and it devastated lots of organisms. Marine organisms don’t do well in fresh water. What that single event did was eliminate two years of urchin recruitment. Urchins recruit sporadically anyway, so it was devastating. That kind of unpredictability makes doing ecology very difficult in terms of a predictive science.

From a marine ecology perspective, are there interesting questions that people are looking at right now?

There are two things, well probably 50, but I will begin by identifying two. Doing the sort of work Daniel Schindler does that looks at watersheds as metapopulations of fish and then trying to protect those watersheds. The production of sockeye salmon varies from place to place and time to time. Daniel’s research is meaningful because it addresses both spatial variation and conservation. For Coho, for instance, 150 years ago there were a lot of streams that were hospitable in the Seattle area. These have gradually disappeared, reducing the metapopulation variation.

Other people are looking at these major fish runs where salmon die and the carcasses are carried off into the woods by all sorts of scavengers and in fact nourish the forest. That’s further essential work.

As a second general issue, a lot of what we study are apex predators. They matter. We should be asking–what are the general consequences going to be when we remove all the sharks from the sea? Or conversely, if the great whales recover, what will those effects be? I have no idea what the answers are, but these are questions we should be asking. The answers change our perception of the whole system from the top down.

There’s an increased emphasis on quantitative ecology and less emphasis on the biological act of going out and getting your hands dirty and really being in the area you are studying. What do you think of that?

Well if you go one-on-one with a limpet you can learn an enormous amount. You can do that. How do you do that with a great white shark or blue whale? There’s this barrier to what I would call natural history. There is a time and spatial dimension as well. People working in terrestrial forests run into the issue of trees that live thousands of years. How are they going to deal with that? These are terribly important systems, but are difficult to manipulate. Dispersal is one of the difficult to measure ecological processes which is critical to document for species or ecosystem recovery. The ecological effects of non-human mediated invasive species is a dispersal phenomenon and is likely to increase, equator to pole, up mountains, as the earth continues to warm. These are important applications for quantitative approaches.

What piece of advice do you wish someone had given to you when you were a graduate student? If you could go back in time and tell the graduate student version of yourself one thing, what would it be?

My graduate career didn’t lend itself to answering that question. I started out in geology because I was deeply interested in paleobiology which was virtually nonexistent at the University of Michigan. My revered adviser said on the last day of my first year there: “Bob, bring your admissions file from geology and I will get you into zoology and accept you as a graduate student.” That was the best thing that ever happened to me. It took me awhile to shake off paleontology. I did my dissertation on brachiopods, terribly important in the distant past, a minor phylum today. I did my work on brachiopods in a soft-bottom situation–both the species and the physical setting doesn’t lend itself to experiments of any sort. On rocky shores you can do almost anything, soft-bottom situations are very difficult.

One piece of advice that I give to all graduate students–well I did my graduate work starting with a hypothesis. The brachiopod I worked on had a fossil record that goes back to right after the Cambrian. I wanted to know–these organisms are basically morphologically unchanged–I wanted to know whether there were any clues that one could garner by studying them, as to what contributed to their 450 plus million years of generic longevity. I did this by going out there and observing and doing my best to quantify things.

My advice to graduate students has always been to go into nature and learn something about the natural history and quirks of the things you want to study. It has to be motivated by curiosity. There is a whole variety of things to study, like sharks, crabs, tide pool fishes, or sea anemones. Then think of some way of manipulating them and posing some hypothesis that you can experimentally explore. If it doesn’t work you are going to have to address the issue of why didn’t it work. Was the equipment wrong? Was the signal too weak?

The best advice is to identify low hanging “fruit” by using your eyes and looking for strong interactors and obvious patterns. And then tweak the system. Your intuition might identify a strong interaction and because of that, suggest that you’re not going to be confounded by the slop and randomness of nature itself.  You might get a result.

Can you tell us about a particularly memorable experience you had doing fieldwork, good or bad?

I won’t tell you about the adventures, in large part because they are inappropriate but I’ll assure you that working on an isolated island on the outer coast of Washington and landing by zodiac on an exposed rocky shore many times during the year proved a lifetime of adventures.

But to answer your question. In the 1970s I got a substantial amount of money from NSF with Tom Zaret to look at the role of invasive species in Gatun Lake, Panama. We had this grand plan for experimental manipulation with the peacock bass which had moved like a wave through the lake, eating most small fish in its path. In front of the wave everything was normal, but behind it there were very few fish left. In front of it there were well-fed tarpon and herons as well as other fish eating birds. We had huge quantities of netting and quartered off some coves and not others in front of the wave of the carnivorous fish coming in. It was a colossal amount of work to put up the netting. We came back later and found that caimans or something like that had plowed their way through the netting. So we realized that the manipulation clearly wasn’t going to work. Zaret went off to do other research but ultimately we got a Science paper out of it, and it’s been cited many times.

But to return to my joy of experimentation. By then I’d discovered the ecological wonderland of the outer coast of Washington and how to manipulate Pisaster (sea stars). I started that work in July of 1963 and by the following spring I knew I’d hit ecological gold. The experiment wasn’t too badly designed, it had a removal plot and a control, but it wasn’t replicated because I was doing all this by myself. Where I had removed the Pisaster the shoreline was packed with recruits of mussels. I spent the next five years protecting them from Pisaster which lead to the keystone species hypothesis and eventually trophic cascades which are some of the important cornerstones for appreciating apex predators and conservation biology.

Did you know right away how big of an impact it would have? People spend their entire lives studying your theories.

Oh yes they do, and that produces its own headaches. But here’s a story. When that (keystone species) paper came out, I ordered 600 reprints, they went instantly. I went back to American Naturalist and got 600 more, and they went instantly, I went back again and they said sorry, they couldn’t print anymore. Later, I went home and  talked with my mother, who at  that time was writing small contributions for the New York Times science page, and I bragged, “Mother! Look at how successful this paper has been.” She said: “Son that’s OK, but I have a story to tell you too.” There was a senator, Bill Proxmire from Wisconsin who liked to make fun of science but was also a good environmentalist. She said, “1200 reprints that’s pretty good, but Proxmire asked me for 200,000 reprints of something I’d written for the NYT on the importance of water conservation, and he wanted to send that out to every voter in the state of Wisconsin” I said, “Mother, I am never going to get into another discussion of this sort again.” They were two very different audiences, and hers was possibly a more important one.

Is biodiversity useful as a scientific subject or conservation target?

Peter Kareiva has it all right. He and I have talked about this extensively. If you don’t know how something works, you can’t fix it. There’s this rivet hypothesis. If you let enough rivets pop out, eventually the plane crashes. It’s not a bad analogy, but it treats every part of the plane as equivalent. My pitch, is if you think of the world as a troubled automobile, do you want someone fixing it who is an illiterate mechanic or a highly educated mechanic who can only read the parts catalog? Reading the parts catalog isn’t going to tell you what the battery does or the starter motor. The real mechanic is going to say, “I know exactly what’s wrong with your car, your battery isn’t working, I’ll get you a new one.” There are minor parts to cars, you don’t need the radio, people use their horns too much but you don’t need those either. Cars have major and minor parts; ecosystems do too. That’s what experimental manipulation can identify, and it begins to tell us how ecosystems are dynamically organized.

All of us who study ecology would agree that ideally we would know everything about how things work before we make decisions about prioritizing conservation targets. What do we do when we don’t have that knowledge but a rivet looks like it might fall out soon? 

You develop a thick skin about the triage that is certain to happen. We are going to lose species. There is nothing honorable about that in terms of the impact we are having on the world.

Do you think it’s better to take a precautionary approach and protect species or take a step back and watch things and monitor?

I think both, but the precautionary principle is fundamental. If you open up the barn door, the cows escape and you can’t get them back in very easily. It’s better to keep them inside until you understand based on observation or some quantification of what the consequences might be. That is what some combination of biological science and natural history allows you to do–make a forecast. You might be wrong, but a forecast is better than no forecast. Think about hurricanes, without forecasts think about the destruction. Now we can warn people that there is a hurricane on the way. The precautionary principle has to be a fundamental obligation for resource managers.

Any parting thoughts?

In those quiet moments that are increasingly rare, I worry about the world we’re bequeathing to our descendants. We’ll probably be able to preserve bits and pieces of it through hard work and dedication but that’s the optimist in me speaking. I occasionally use the phrase that environmentally “we’re going to hell in a hand-basket”. The biological and physical sciences have done and will continue to do an excellent job in quantifying this decline and in describing the whys. I’ve excessively enjoyed a lifetime of observing nature, bird watching, gardening, teaching and research but by 2100 will that have made a bit of difference? I don’t believe so, and worry that these great pleasures, both personal and academic, will be increasingly difficult to achieve. A diminished nature will surely be present but I suspect it will be more boring, less stimulating. Ecologists will have to become time travelers to practice their brand of science.


September 10, 2013

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  • I really appreciate Bob’s perspective on humility in the face of ecological variance, and in steeling ourselves to face the coming decades/centuries/millenia of global ecological disruption.

    I’m now curious about what his recommendations might be for how the Precautionary Principle should be implemented in resource management. What level of precaution is enough/too much? For instance, does it extend (as some would argue) to trying to avoid, manage, or eradicate all invasive species?

    • Probably a lot of population and community ecologists agree with him about NEON; I know several people who do. It’s not as if I’ve taken a random survey, so I wouldn’t venture to guess what proportion of ecologists agree with him on NEON. But I think it’s a non-trivial proportion.

      As for “big data”, I think it depends what you mean by that. One can certainly test a priori hypotheses on big datasets (however collected or compiled). Whereas it sounds like what most bothers Bob about NEON is lack of hypotheses determining the choice of what data to collect. I suspect Bob would find hypothesis-free research problematic whether it involved collection of “big data”, or only small data.

    • Full disclosure: I work for NEON. But I come at this question with a personal interest in the history of big science and the culture of science.

      The International Biological Program (IBP) that Paine cites was a big-picture ecology project that was widely considered a failure. But that doesn’t mean the project goals were meritless; it just means that the approach was unsuccessful. Some notable UC science historians have researched and discussed what the IBP project did and didn’t accomplish, and why:


      Aronova, Baker and Oreskes write that the original IBP (which ended in 1974) was far too decentralized to achieve its goals. But, they add, IBP ultimately became LTER, and in the process 1) morphed from a short-term project to a long-term one, 2) pioneered a lot of large-scale collaboration and resource-sharing frameworks in ecological research, and 3) attained many of the goals that the original IBP didn’t.

      I’ll echo a point that many have made before me, that LTER and other recent projects probably helped lay the cultural groundwork for something like NEON – a centralized, large-scale, long-term synoptic data collection effort. I know many ecologists, biologists and environmental scientists don’t have the desire or skills to do data-driven science or work with large, shared data sets — but plenty do. I meet them every year at ESA and AGU, on Twitter and via projects like DataONE and NCEAS. It seems a lot has changed both culturally and technologically in the 40 years since the IBP.

      • I agree with all of the points here, but I get the impression that Dr. Paine was lamenting the supposed lack of cooperative research networks with targeted *precise* questions that employ an experimental vs observational approach. But even then, I can provide two examples of global experimental networks that do, NutNet (http://www.nutnet.umn.edu/) and ZEN (http://zenscience.org/). I expect (and hope) that these two (and others I may not be aware of) will set the precedent for doing relevant, hypothesis-driven research on global scales.

      • Good examples, Jon. I would like to hear Paine’s take on NutNet and ZEN and see if it’s consistent with what he said here.

        I agree with Jeremy that Paine seems to have issues with data that aren’t collected with a specific hypothesis in mind. I’m disputing Paine’s premise that the IBP is proof that all large-scale ecological data collection projects are useless, but I’m not well equipped to argue the value of data collected without a specific hypothesis in mind — except from a cognitive science point of view. We all have well-documented emotional and cognitive biases, no matter how objective and rational we like to think we are. Collecting data with a mind to supporting or refuting a stated hypothesis might predispose us to classic confirmation bias in the interpretation of our data. And confirmation bias might have something to do with a strong affirmative publication bias in scientific literature. Not to mention the whole “publish or perish” thing.

        It’s also worth pointing out that NEON isn’t just data [WARNING: shameless plug starts here]. It’s a network of standardized field sites and baseline data upon which researchers can build experiments and analyses that test specific hypotheses on a larger spatial scale and longer temporal scale than would be possible with a given budget and without that sort of infrastructure already in place [http://neoninc.org/contact/requestresources]. It’s also a collection of documented specimens (organisms, soil, etc.) that researchers can analyse to test specific hypotheses. [shameless plug ends with link to soil archive http://neoninc.org/science/soil-archive.

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