Some may know UC Berkeley professor John Harte from his work developing the MaxEnt Theory of Ecology (check out July’s TREE for an accessible pedagogic overview), others may be more familiar with his long-term research on the effects of climate warming. Older readers likely recall his 1988 classic book on environmental problem solving named after an improbably shaped bovine. I had the opportunity to meet and chat with John at the recent Gordon Research Conference on Unifying Ecology Across Scales, where he and Mike Sears gave very interesting and divergent opening talks on how ecologists might bridge the problem of scale for a more productive science.

Could you give a brief overview of your scientific philosophy and how you approach science?

The very most important thing to me, being a scientist, is to seek out unification- to look for simplicity where initially we see nothing but complexity, and to see the underlying general principles that govern the phenomena of interest. In ecology we have a wealth of phenomena… everywhere we look we see uniqueness, but being a scientist I refuse to accept that and I look for what general underlying patterns and principles govern this wealth of phenomena. And so, to seek that, I love looking at huge databases and I love walking in the woods and observing patterns and the details. But, my major approach to seeking unification is to develop fundamentally-based theory.

Can you explain what you mean by a fundamentally-based theory?

I know a lot of people in ecology love to make models of phenomena. You see some behavior, you see a particular species dwindling in numbers on the edge of extinction and so you make a model of that phenomenon. Or, you see a funny pattern where you see some sort of regularity in who’s associating with whom, and so you build a very mechanistic process-based model to explain that behavior. Out of the thousands of possible traits and mechanisms that might be working, we use our intuition and pick two or three that we think are important and then we build a mathematical model and it’s got parameters so we show that if we pick the parameters right we can explain the behavior. I find that totally uninteresting. That is not what I do. But it does characterize a lot of good and important work in ecology. It’s just not personally what turns me on. What does turn me on is seeking out very general principles that must be true from which very general conclusions can be based, which can be tested, which are falsifiable, and which potentially, if the theory is right, can explain a huge amount of information.

As an example, I’ve always been very interested in species-area relationships. I think they encapsulate a huge amount of information. Now, if you look at all the known species-area curves in the world, of everyplace where somebody’s gathered species-area data, and you plot them all on one big piece of graph paper- log species vs. log area, you will find that the data points fill the graph almost completely. You get every possible behavior when you just do a plot of log S vs log A. There’s no regularity. I didn’t really think that had to be the case. What I learned from developing the theory of macroecology based on the maximum-information entropy principle, is that the theory makes a very startling testable prediction about the shape of the species-area relationship. It says that if you take any species-area curve and you plot the local slope of the log-log plot, what we call ‘z’, at any scale against a certain scaling variable that the theory identifies, namely, the number of individuals at that scale divided by the number of species at that scale, all species-area curves should collapse onto a single universal curve. And it turns out that they do. If you look at every species area curve in the world, there are no exceptions. Even ones that involve microbial species-area relationships like the one my former student Jessica Green developed. So we think we understand the species-area curve. It’s not a power-law- it obeys a universal scale-collapsed behavior which theory, not a model, predicts. To me that was a significant break-through, to be able to see that all species-area curves fall onto one universal curve if you re-plot it correctly. And the neat thing is, it’s not just something we guessed. The theory told us we had to re-plot this way.

Has your approach to science and scientific philosophy changed since you were a graduate student in physics, or has been a theme throughout?

It’s been a theme. When I was a kid, my major interest was bird-watching and natural history. I collected everything I could collect. My bedroom as a kid was a museum. It was extraordinarily overstuffed with fascinating little things I would find. I would catalog them and arrange them and study them. But even then I remember thinking, “where’s the simplicity behind all of this detail?” I went into physics partly because I thought that that was a branch of science where you could freely exercise this desire to seek universality, generality and unification. Physicists are very open to that goal- that’s what they do. My first faculty position was at Yale University and I realized 6 or 7 years after my PhD that I really wanted to go back to what I loved the most, which was biology and especially ecology. So I left the physics department and took a job as an ecology professor at Berkeley in the early 1970s and I’m very glad I did it. But, I’ve been pursuing that same theme, that same interest, all the way through, from childhood birdwatching to physics and back to ecology.

Was there something in particular that made you realize that you wanted to go back and do ecology or was it a gradual realization?

No, it was a very specific thing. During the Vietnam War, I co-organized a day of teach-in’s about the war, where we shut down all the science classes at Yale and we brought in speakers to educate ourselves, the faculty and the students, about the war. At that event one of the people I invited was a very famous physicist, a Nobel laureate who had gone to Yale as an undergrad, and at the dinner of the teach in, he asked me if I would be interested in joining a small group of physicists who were going to try to do something about environmental issues- take a summer or a year off from regular physics and see if we could make some headway. So we did. We studied a problem in the everglades of Florida, where there was a proposed super-sized jetport being planned to land the super-sonic planes that we thought we were going to build. So we studied the Everglades. We took 3 months and did nothing but immerse ourselves in the problem. I ended up writing a paper with a colleague that looked at what would happen if you drained all the marshes in central south Florida where the big jetport complex would be. We were able to show with a little bit of physics that it would lead to salt intrusion into the water supplies of over half a million residents of the Gulf Coast of south Florida. That reached the desk of the secretary of transportation who said to Nixon, who was president at the time, “We can’t build this jetport- we can’t throw away Florida in the election, and you will if you destroy the water supply of half a million voters.” So they canceled the jetport. So I actually got back into ecology with the major goal of doing very practical applied work to prevent other disasters, like wrecking the Everglades. But then as time went on I got more and more interested in big theoretical questions.

Given your initial reason for moving back to ecology, how do you see general theory, and in particular the maximum entropy theory of macroecology, informing conservation or more applied work?

Great question! I have a post-doc, Justin Kitzes, a brilliant guy, who is doing exactly that (see ‘Continuing the Conversation with Justin Kitzes’). His main interest in conservation biology, but he’s really a good theorist too. So he’s been taking the predictions of maximum entropy theory and applying them to very practical questions. Questions like, ‘What is the magnitude and origin of this ‘so-called’ extinction debt?’, and ‘How many species do we lose if we deforest a portion of the Amazon?’ People have realized from way back that the species-area relationship has something to do with that, but now that we know the true behavior of the species-area curve, we can very accurately estimate species loss under habitat destruction, or under loss of climatically suitable habitat. Another question that Justin and I have been looking at that is not exactly a conservation issue, although people have been fascinated by it, is ‘How many species of beetles are there in the Amazon?’ All we know is that we’ve labeled about 1.8 million species total, but we think there are way more than that. We have a paper in review right now that projects out from small plot data using the species-area prediction, what the species richness is at very large spatial scales. So we make predictions and they may or may not be of conservation value, but I think it is useful to have a measure, to have a sense of how diverse our planet is.

In your talk at this conference, you said that a scientist should “sleep with his theory but not be married to it”. Can you expand on this? How could this philosophy contribute to either scientists’ or society’s thinking about biodiversity and conservation?

I think science progresses from failure not from success. It’s failure that drives science forward. For example, when there’s a discrepancy in something that we always thought we understood and then realize our theory is incompatible with some new phenomena, and we say, “That theory is not correct!” And that’s what make science move forward. That’s how progress happens. So, my view is that, there is nothing more important, nothing we should look forward to more than discrepancies between our favorite theories and reality. Because then we improve. We figure out what the next step is.

A very famous example in physics was the ideal gas law, PV = nRT. It’s a very basic idea from thermodynamics and it’s a beautiful law, but it actually fails at very high pressure and very high temperature. Its failure led physicists to realize that there was something called dipole-dipole forces between molecules, a very important thing in physics. And it was only from the failure of a prediction that they were led to discover this mechanism. Openness to failure and being willing to revise, upgrade, and form the next-generation theory is very very critical. So that’s what not marrying your theory means, don’t get so wedded to it that divorce looks impossible. As far as how that idea helps connect people to biodiversity, I’m not sure it does because we are in a sense all married to biodiversity. Biodiversity is what drives the human economy. Ecosystem services are dependent on diversity and the human economy is dependent on ecosystem services, and we should think of that as a catholic marriage that you can’t get out of. You can’t divorce yourself from the natural world. Unfortunately, civilization acts as if it’s trying to divorce itself from biodiversity and nature.

Ecologists and evolutionary biologists are constantly borrowing concepts and methods from physics, but many ecologists have a limited education in physics. Are graduate programs failing to provide necessary physics literacy to ecologists? What could be done about this?

Oh boy, don’t get me started… It’s actually appalling how little math and physics ecology students have. Not all, some come in very well prepared. But, I firmly believe that departments of ecology and evolution should be requiring more of their students to take at least one theory course with mathematical methods, stochastic modeling, more than just the basic Lotka-Voltera equations, which is about all most ecologists ever learn. I mean, those equations are sort of a good laboratory for introducing oneself to quantitative reasoning, but stopping there is not adequate. We require a good deal of statistics on the part of our students, but that’s not the most important kind of math. Students should also be learning stochastic mathematics and probability theory, using differential equations to study things like stability. There’s so much confusion about these things and if students were better educated it would make for better grad students.

On that note, what do you hope for the next generation of scientists that are currently graduate students? Is there something you would tell them? Some direction you would point them in?

I see a couple of risks on the horizon. One of them is the ease with which we can simulate numerically and handle massive data sets. There is a risk that this will divorce people from what really matters, which is the natural world. Ecologists who are incredibly adept at manipulating data and running simulations, but who never just walked in the woods, observed and in their minds sorted and catalogued the things that they are seeing, those students have a great handicap in the long run. Separation from the natural world because the silicon world is so easy to enter- that’s very dangerous. The other dangerous thing is that we get obsessed with mechanistic tinker-toy models and do not look beyond to the broad fundamental theory, which doesn’t require computer adeptness or capacity to manage big data sets or simulate numerically. Fundamental theory really is more a matter of thinking through things than running amazingly complicated programs. Think of three vertices on the triangle. There’s the real world, nature, there’s what I call theory, and there’s the silicon world. I’d like to see people spend most of their time on the leg between the theory vertex and the real world vertex and only when you are forced kicking and screaming, go to the silicon world and simulate.

Other scientists we have interviewed philosophically place much less emphasis on searching for general ecological laws. As someone for whom the search for generality is paramount, what do you see as the purpose of knowing general ecological laws?

From general laws flow absolutely bullet-proof insights and this is what we most need. To the extent that ecology can be based on broadly applicable laws, not models based on arbitrary choice of dominant mechanisms (which everybody will argue about until the cows come home), if you can base insights and predictions on laws, they are irrefutable and that’s how science can best influence policy. Ecology is not in good shape when it comes to influencing policy. For example, if an asteroid is going to hit the planet, congress will call upon and believe the physicists who can calculate the likelihood of impacting when, and maybe even what to do about it, because those physicists can base their statements on fundamental laws. Ecologists don’t get called or listened to when it comes to any big issue. We don’t have respect in policy circles because we haven’t figured out the laws of ecology. Instead we have a gazillion models of ecology, stories, and intuitions. Some of them are right, some of them are wrong, some of them aren’t even right or wrong, they’re not even testable, which is even worse than being wrong. The need for developing fundamental theory is just huge. If we’re going to save the planet, I think it’s critical that we do.

What have been opportunities in your career that have been unexpectedly valuable?

Besides theory, I like to do field work. I hate lab work- my students won’t even let me in the lab. I spend summers at the Rocky Mountain Biological Laboratory and this is my 38th consecutive summer. Twenty-seven years ago, I had this idea that everybody tried to talk me out of, which was to set up an outdoor climate warming experiment. We set up this big bank of overhead electric heaters that radiate heat down onto the ground to simulate the climate of the year 2050, roughly give or take. We have been running this now for 25 years. The heaters are on summer and winter, day and night. It’s the longest running experiment of its kind. But, when I set it up I got all kinds of arguments that this was a stupid thing to do. The first proposal to NSF, I got a review back that said “It won’t work because as the heat radiates down to the ground the wind will blow the radiant heat away.” So they rejected the proposal. I wrote back to the program manager and I said, sarcastically, “Oh, so that explains why when I go out at night with my flashlight and it’s windy the light beam doesn’t hit the ground, it blows away.” And the program officer wrote back and said “Oh. I see what you mean”. They had rejected the proposal by taking the word of a reviewer that it wasn’t going to work and they didn’t know enough physics to understand that electromagnetic radiation doesn’t blow away. So by persevering, there have been 33 journal papers that have come out of this one experiment, 9 PhD theses, and over 100 undergrads have gotten their field training with me doing this. It certainly is the single biggest field experiment I’ve ever done. I’m glad I persevered- that opened up so many doors for me and for my students especially.

Do you have parting thoughts?

Well let me ask you a question. What do you think are the similarities and differences between ecosystems and physical systems? Some people say physical systems are really basically simple and ecosystems are intrinsically complex. Does that resonate with you?

Yes, readers, he means you too! I’ll refrain from sharing my own muddled reply. Tell us what you think in the comments. Or, read on for John’s answer…

Well I’ve been thinking about this a little bit. That there is a system in physics that everybody agrees is mind-bogglingly intractable, and that’s turbulence. Now the thing about turbulence that makes it interesting is that it’s a phenomenon that occurs at all scales. Little turbulent eddies become bigger, become bigger, BECOME BIGGER, and finally become huge atmospheric vortices. It’s why climate is so hard to model in detail- because you can’t make clean scale separations. Now my view is that complex systems are systems where you can’t make clean scale separations. So, the question is, can you in ecology? This is what we’ve been trying to demonstrate with workable theory. That you can think of the trees and the forest. The forest is the macroscale, the trees are the microscale. You could go to a lower microscale like cells, but let’s stop with the individual trees as the simplest unit in ecological theory. If you do that, you can apply ideas from statistical physics and scale separation works. It’s a simplification, because there are phenomena within a forest that are smaller than the forest but bigger than the tree, associations between trees and so on, but, to a first approximation you can make that macroscale-microscale separation. You can’t do it with turbulence. So if that is a correct way of thinking, it suggests that we’ll have an easier time with ecological theory than we would with a theory of turbulence.

August 31, 2014