Hari Sridhar: The motivation for this interview is the talk you gave in YETI in 2009, which was in the form of advice to young ecologists on how, you think, science should be done. One of the points you made that stayed with me for long after the talk was about making the transition from being a student to doing research – from taking courses to doing research – which you said involves a process of ‘unlearning’. Can you tell us a little more about what form you think this ‘unlearning’ should take?
Raghavendra Gadagkar: One of the points I emphasised was how to make the transition from taking courses and passing exams to doing research and making discoveries. And I said that if you want to make this transition you really have to turn around 180 degrees, because the optimum strategy for being successful in taking courses and passing exams is quite the opposite – not just different but the opposite – of the optimum strategy for making discoveries. For example, if you want to take courses and pass exams then it makes sense for you to place yourself in a place where you are comfortable. For example, you have an exam and you know that you are going to be given six questions and you have to answer any four. It makes sense for you to focus on the four where you are most comfortable. It doesn’t make sense for you to say I know the answers to these four, I don’t know these two, but I am going to try and answer these two. But if you are doing research that is exactly what you have to do. It doesn’t make any sense to say I know this therefore I am going to work on this area. You have to work on what you don’t know. You have to move away from the comfort zone of knowledge and familiarity and position yourself in the discomfort zone of ignorance and unfamiliarity. In other words, you must enjoy feeling stupid. If you say that it’s frustrating because you don’t know what’s going on then you are probably not cut out for research. Also, for taking courses and passing exams you often have to focus on storing information and recalling at the right time, which is not at all useful for research. Now that is easy to say – most people will agree with that – but the problem is much deeper and psychological. Our entire social structure is built on great prestige for knowing facts and great shame for not knowing facts. Somehow, thinking is not part of our social culture. I guess that’s because for most things you don’t have to think – somebody has thought it for you. You just have to know what it is. In research obviously that doesn’t work. You have to do exactly the opposite and you have to learn how to think de novo.
There is another problem with doing this, which is that you need one kind of mental energy to absorb facts and recall them and a very different kind to be able to think through something. These two are not the same. You can train yourself either to do this or to do that. Seldom can you do both; there is a trade-off between these two. Take the example of those people who become crorepatis after answering all those questions on quizes – they are really optimised so that they can store and recall efficiently. They can’t think. And that’s a good thing when you are taking exams and doing courses. In fact, all said and done, in most exams thinking is still a minor thing. In fact even if it is required, you also need to remember lots of facts in order to do the thinking. In research you don’t have any of those problems. So if you want to optimise yourself for thinking, then you have to tell yourself you don’t need to carry the facts with you. You can get them whenever you want. If you clutter your table with all the supplies you have in your house you can’t cook. So all the items should be in their shelves and you take them out whenever you want them and then put them back. You should have space to cook. The equivalent shelf is your library or the internet. Take it, use it, but keep space in your brain to do the thinking. But in order to do that you must get over this feeling of pride in knowing the facts and feeling ashamed of not knowing them. I tell my students: do not be proud that you know something and do not be embarrassed that you don’t know something. In fact, I go to the extent of saying that those of you who already know the facts are the unfortunate people because once you know a fact it’s very difficult for you to actually derive it de novo. It’s very hard for you to walk that path. Your mind refuses to do that. Also it’s very boring. Imagine somebody gave you a really nice mystery novel and says: I recommend you read it and btw that’s the guy who actually committed the murder. You will not want to read that book. You will want to read that book because you want to know who the killer is. That’s what drives you to read the book.
So I often tell my students that I won’t give them facts but I will teach them how to think. But in order to do that I have to find a topic where they don’t know the answers already. And I must confess that it is becoming increasingly difficult to do so. Due to the internet, now students know everything. They don’t know how to get there but they all have the final answers. So I have to find something that they haven’t heard of. And then what happens in a typical class is there are a few students who know it all and are eager to answer and I have to keep them down. I always look for that student who doesn’t know the answer so that I can demonstrate through that student, to the others, how to find the answer de novo. Sometimes it gets very funny. A student once told me: There’s something wrong with you. Yesterday I knew the answer and you didn’t let me answer. Today I don’t know the answer and you are harassing me. But that is exactly the point. It is by ‘harassing’ the student who doesn’t know the answer that you can demonstrate how to find the answer de novo to the unfortunate guys who already know the answers. So I keep telling them, that when I am ‘harassing’ this student the others can’t go to sleep. This student is the altruist who is going to help you learn how to walk this path that you are no longer capable of walking because you already know the answer. What does that mean? That means you shouldn’t read too much, because you have closed the doors for everything that you have read and got the final answer for. Even as an experiment in learning how to think, that territory is no longer available to you. So there is an optimum amount of reading that you should do. And your reading, as far as possible, should be around or outside your field. If you want to do research, you shouldn’t read on too much in your topic, but around your topic, so that you can bring new perspectives to bear on the topic. If you read all there is to read on your topic you will probably do the same thing that other people have done. It is very hard to think of new ideas. Every idea you can think of has already been thought of.
But even more than that, the real problem I think is that, given the way our brains are constructed, it’s much easier for us to master the art of remembering – of inputting and outputting facts. I think our brains are not constructed to think very much, and another big problem in thinking is what I call mental laziness. Very quickly you are lazy to think further. Let me take an example. In an exam a student is copying from his neighbour. Now, Step 1 is that the student knows that he is copying. Step 2 is that the student knows that I have seen him copying. Step 3 is that the student knows that I know that he knows that I have seen him copying. These are three different things if you think about it. If the student has copied and nothing else has happened that has one consequence. If the student has copied and I have seen him that has another consequence – I can punish him but he doesn’t know that. If he knows that I know, he will stop copying, otherwise he will continue to copy – do you see these are three different things? Now with some difficulty we can manage these three levels. But you can take it to a fourth level – do I know that the student knows that I have seen him copying? If I know that the student knows, then I know that he is going to stop copying and therefore I must do something else. Now you can take this to infinite steps but try doing this and your mind gives up very quickly. Three is difficult, four is about the limit, and after that it’s all muddled up, because of mental laziness. And that is what we need to avoid. But that’s not a problem when you are taking course and passing exams. So doing research is a very different game. Unfortunately, we do not train people to do research. We mailnly train people to take courses and pass exams.
HS: You say one shouldn’t read too much. Is there the danger of going too much in that direction? One would imagine that to be able to come up with new ideas, to be creative, you need to be able to make connections between facts, and those connections might not happen unless you have those facts in your head.
RG: I have the following model. I make the assumption that anybody who wants to do research is a reasonably intelligent person who will read x amount of stuff in a 24 hour period. All I’m saying is that as large a fraction of that x as possible should be outside and around your field, outside your problem. I am not saying you shouldn’t read. Then, of course, you are not able to think, but as far as possible the reading should be outside. In research, you don’t want to do what others have already done. You want to do something different. You want to come up with a different theory, a different answer. In research getting a correct answer is not important, getting a logical answer is important. You don’t know which answer is correct. Ultimately, if all these hypotheses are put to test then something turns out to be correct. We don’t reward people for being correct, we reward people for saying something new. For doing something that’s creative. Therefore, the best strategy is to do what others are not doing. And you can take for granted that most people are working very close to the centre of their problem. So the further you go with your reading, the more the chances are that you will have a different perspective from others. And that’s really what matters. So it’s not the absolute amount of reading, but the distance of your reading from the actual centre of your problem that matters.
HS: You said in your talk that people who are good at doing courses might not be good at doing research, that there is unlikely to be a strong correlation between the two…
RG: Let me refine that a little bit. I think there is a trade-off between doing well in courses and doing well in research. But I wouldn’t say that people who do well in courses will not do well in research. I don’t think people are fixed. If you have trained yourself to do well in courses, but are unwilling to unlearn then you won’t do well in research. But if you are willing to unlearn and now have a new strategy then you can do quite well. There is a trade-off between the strategy to do well in courses and the strategy for doing good research but it is entirely possible that the same person will be able to change strategy. So this has relevance to the question you were asking about how one should pick candidates for a research programme. If there was a simple one-to-one correlation – a person who is good in taking courses and passing exams will not be good in research – then of course it is very easy. You give an exam based on courses and whoever fails you take for research! But it doesn’t work like that because some people are able to change and some people are not able to change. Also, some people are so intelligent that they will be able to optimise the strategy required for passing courses, but then shift to the strategy to do good research. That is what makes it much harder to select people. You can’t simply say I will take the people with the lowest marks. That’s not going to work because the people with the lowest marks might not be capable of doing either. People with the highest marks maybe capable of doing both, but also may not be. And then there are people who are very poor in taking courses and passing exams but actually very good in research. So you have to work very very hard in selecting people. And the one way to do this is to actually put them to a test in thinking during your selection process
HS: Which is difficult given the number of people who apply..
RG: Not so difficult. Ideally, take them outside their zone of comfort and see whether they can think. It is not so difficult. In 30 minutes you can judge whether a person is capable of thinking. It depends on how you spend those 30 minutes. What we typically do is for 25 out of 30 minutes we ask them for the facts they know, and for barely 5 minutes we ask them to think – that is the problem.
HS: But what you are suggesting is possible only with a smaller subset of shortlisted candidates. How do we do the first step when a large number of people apply?
RG: I think you need a minimum of 30 minutes – ideally an hour. So if you are willing to spend 50 hours you can only have 50 to 100 candidates. But you will have to have some other method to bring the first set of applicants down to 50 or 100. I don’t think there is any way of getting around that. But of course you can design written exams that test thinking abilities rather then recalling of facts.
HS: You said that while in an exam it pays to choose the easiest question, in research it might be best to choose the one we know least about. I would like to ask you about your own strategy when it comes to choosing a research question. What makes a particular topic worth pursuing for you?
RG: The answer should not be obvious and it should not be so obvious that you will find the answer rather quickly! Only then it’s challenging, otherwise it’s not. Having said that I must also say that in real life, for my own research – this takes us off into a completely different territory, so we won’t go there just yet, but I’ll just say – I have chosen to understand everything humanly possible about one species of social wasp. That is my decision. That’s what I want to do. So in trying to fulfill that decision I’m not always in the position of saying shall I answer this question or that question. I need to answer all or most questions in order to go to the next level. So in real life I don’t always discard questions because they are easy or obvious. I do them quickly. But I find much more challenging, those questions where the answer is not so obvious. Often there are lots of little, not so interesting, questions that you have to answer to be in a position to get to the big, more interesting and more challenging questions.
HS: You have been working with this one species for over 30 years. Right from the beginning did you know that this was going to be a long-term research interest?
RG: Not in the beginning, but very soon it became obvious. See, I had been playing with this species for a long time, but I will say that I seriously started working on this species roughly in the year 1980. And in 5 years it was clear to me that there is enough gold here that one can spend one’s whole life in it. It took about 5 years, not longer than that.
HS: Going even further back, when did you first realise that you were interested in doing research?
RG: Oh that was very long ago. I probably didn’t know the meaning of research at the time that I realized that this is what I wanted to do. I mean I was curious and interested in science. But again there was this problem: I never thought that science has to be done in exclusion of other things. It never occurred to me that if I did science I couldn’t do literature. I found it very funny. In those days, you had to choose in 8th standard – science stream, arts stream or commerce stream. I was completely lost because the two subjects that I was extremely interested in, and which I thought I will pursue for the rest of my career, were science and Hindi literature. My Hindi teacher thought I was born to do MA in Hindi and my science teacher thought I was born to do a PhD in science. I thought I am born to do both! But I had to very very reluctantly drop my dream of studying Hindi at that stage. And then when I came to biology they said maths or biology! So I had to drop maths. And then afterwards they said molecular biology or animal behaviour. I said I want to do both. They said you can’t do both, you can only do one. The higher I went, the more doors closed – very strange indeed.
HS: Going back to your own philosophy when it comes to choosing research questions – the pieces of the puzzle, not the big questions – do considerations such as doability, money required, technology required etc. play a role in your choice?
RG: Absolutely. And I think the biggest mistake that people make is they do not do what I call a feasibility analysis. You are a postdoc in NIH, you are working on a problem, and you bring a little piece of that problem and come and join some place in India and want to do the same thing. You are not worried about whether you can do the same thing with the same level of competitiveness; you do not worry enough about what you will need, how much money you will need, what kind of facility you will need. Nobody worries about these matters, or at least not enough. They start off and then they complain. I think that’s the biggest problem. What you need to do is choose a research problem where the rate-limiting step is only your intelligence. That’s what should actually finally stop you, not money, facilities or anything else. If you choose a problem where the rate-limiting step is your intelligence, then you will not be frustrated. You can say this is all I could do because that’s all the brain I have. Whereas if you say: oh, I could have done so much better if I had more money or if I had that equipment, that’s a ready-made excuse not to do very well.
But again one has to qualify this. In the real world, the time when you should adopt this philosophy is not when you are a PhD student; instead it’s when you become an independent scientist. In most cases, I think a PhD programme is best treated as an apprenticeship. I will give you an example. A friend of mine once sent me a message saying he went to one of the branches of the National Museum of Natural History and met a young person who was very interested in spiders. That person said that nobody was helping her and he asked her to write to me. So she wrote to me and said she had some very interesting ideas for spider research, but was very frustrated because nobody was able to help her. I told her I didn’t know too much about spiders, but she should come and visit us for a week. So she came for a week and outlined her research plan and then said it’s so frustrating that nobody is working on this! I said you should be frustrated if somebody is already working on your idea. If nobody is working on your idea, how nice! I told her she is thinking that she will be somebody’s assistant to work on her problem, but why should she? I told her she should safeguard her idea and acquire all the skills that she needs to solve that problem later, when she is an independent scientist. Your PhD or postdoc is often only meant for you to acquire the tool kit that you need for your research career. You don’t have to do your best work when you are a student or a postdoc. And in today’s modern science where you need lots of techniques and skills to be able to tackle a cutting edge problem, you should use your PhD and postdoc to equip yourself with those skills. But what most people do is either they hope to do Nobel Prize winning work in their PhD, or they get locked on forever to the problem that should only be used for training. See if you want to come to my lab and learn a technique, then you will have to work on my problem. But then you should not get stuck with my problem and spend the rest of your life on my problem and forget your own problem. So one must learn how to use PhD and postdoc. time effectively. I once had to tell my student- don’t try to get a Nobel Prize for your PhD work, because most likely you will have to share it with me! If you wait you might get it by yourself.
HS: Did these considerations – money required, technology required etc. – go into your decision to work on Ropalidia?
RG: Absolutely. It was clear to me that the rate-limiting step should be my brain. And till today that is the rate-limiting step. In the beginning I very consciously said I am going to create a situation where the rate-limiting step, not for quantity but for the quality of my work, would be my ability to use my brain. Not anything else. So there’s no excuse if you fail, otherwise you always have a ready-made excuse even before you start. People say: oh but he is in Harvard; you can’t expect me to do as well as him. You start with the assumption that you can’t do as well as him. For me, there is no excuse in the world I can give why anybody else in any part of the world should be able to do this better than me. I can’t think of an excuse, except that I didn’t think of it or am not capable of doing it.
It also depends on where you are. Of course if you end up in NIH you can choose different problems, but even there you must make sure that the rate-limiting step is your brain and not how much money you can get. You may get 10,000 dollars or 10 million dollars. The trouble with scientists is, instead of saying: you tell me how much money I can get and I will think of a creative scientific problem for that money, they say: you tell me how much money you can give me and I will find a problem for which that money is not enough! I believe that you can do creative work at any level of facilities or money or whatever. Problems will change, but not the creativity.
HS: But there are external forces that make people use the approaches/technologies that are in fashion, e.g. the pressure to use molecular approaches in ecology today?
RG: That’s correct. But I would put 10% of the blame on the people who put the pressure and 90% on the person who succumbs to the pressure. I would not absolve people saying don’t blame him it’s the pressure. What efforts do people make not to succumb to pressure? I think we do very very little to avoid doing what we don’t like to do. We immediately succumb to pressure. Often we succumb to imagined pressure. And even if it is real pressure we do precious little to fight the system. So I’m not convinced by this argument.
What have people done to fight the system? That’s why the system doesn’t change. Whether it is pressure to use latest technology for the sake of using it, to publish in Nature whether or not your work is good enough, or to have a collaboration with some famous person whether or not it is required. All this pressure is real, but I have not seen people fight it enough. I have seen people succumb to the pressure too easily, and once they succumb, they want the rest of the world to believe that it is not possible to resist the pressure. So they create this myth and the pressure builds up. It’s a self-fulfilling prophecy.
In fact it is probably very nice that there is all this pressure for people to do the wrong thing because then I can fight that and be different from others. After all, what is the route to success? Doing what other people have not done, not succumbing to pressure, is in fact the route to success. You succumb to pressure you become like everybody else. Your goal is not just to become assistant professor, but to be different from others. Ninety percent of people who are assistant professors become associate professors. If that’s all your goal is, then there is no problem. But that should not be your goal. People who complain that it is the system, it is the society, it is the peer pressure, which makes us do all of this, I don’t buy any of it. I’m extremely sceptical of it. I rarely come across people who resist pressure. People always succumb to pressure and they complain. I want to see more examples of people who resist pressure.
HS: I want to talk about another kind of pressure – the pressure to publish in high-impact journals. How do you decide where to send the papers you write?
RG: There are only two things that matter to me. One is, as far as possible, it should go to the audience I would like to reach. Today, that is becoming less important because you put it on your website and people will see it. So what is the most important consideration? It should get published, it should not get rejected, which is the opposite of a typical strategy. The typical strategy is, no matter what you write, you first send it to Nature. When it gets rejected, you send it to Science. It gets rejected then you send it to PNAS. And then it will trickle down after 3-6 rejections till it finally finds its level. This is what people do. This is hugely wasteful for everybody. The first problem is that the top journals like Nature get all the papers in the world! So they have to reject 99%. It’s a huge waste of everybody’s time. In fact I actually know people who say: I sent a paper to this journal and it got accepted. What a shame, I should have sent it to a higher journal! This is the world we live in – completely crazy. I would like to send my paper to a journal where it has the highest chance of getting accepted. Now if you want to increase that probability what do you do? You send it one step below what you think it deserves! I will tell you a story about one journal. At this journal they reject whatever they don’t like, but of the things they like they publish a few and for the others they say: this is not good enough for our journal but we have a sister (step-sister?) journal which we can send it to. If you say yes, it most likely will get published there. I was surprised by this because I felt how can that journal tolerate this? That you are the trash basket for the bigger journal. So I met the editor of that journal and asked him. But he said no, it’s so easy for us because we get papers that are reasonably good and that have already been refereed and we just publish them. Then I told him who I was and he said: Ah, you are one of few guys who send their papers directly to us. In the long run does it really matter? The idea in your paper is what matters. Think of what might happen a hundred years from now. People will not look at your paper because it is published in Nature or in Science, but for the idea it contains. Can anything be more stupid that judging the quality of work depending on where it’s published? Can you think of anything more absurd? Recently I heard this very interesting statement. Somebody said “just because our paper is published in Nature doesn’t mean it’s wrong”! But I don’t even blame Nature. From their point of view they are doing the right thing. It is we who have sold our souls. How can we let this happen?
I will tell you another story: some years ago I was invited to give a talk in Arizona state university. Before my talk they wrote to me saying: you have some free time and here is a list of our faculty in the life sciences dept. Is there anyone here you want to particularly meet and have a one-on-one meeting with? I looked at that list and in fact most of them were my friends. So I wrote back saying I know all of them and I can’t choose any one or two for having one-on-one meetings. Instead give me a one-on-many meeting with your students. They said this is great and all the PhD students and postdocs of the dept. were scheduled to meet me for 2 hours over a pizza lunch. So we talked mostly about these kinds of things. And then some of them said: it’s very easy for you to say all this, but we are students. We have to succumb to this pressure of publishing in high impact journals because otherwise we won’t get jobs. So I said I agree with you, you are absolutely right. I said: for advancing your career you do whatever you want, do all the ‘wrong’ things that the system wants you to do, no problem. But very soon you will be sitting on the other side of the table to judge others. I am only asking you to make this resolve: you will not judge anybody by the journal in which he or she has published, by the impact factor or by the H-index. If you agree to do this the world will change in 10 years. But the world has not changed because you will begin to believe that what you have done by succumbing to pressure, is the correct thing to do. So when you say you know this is wrong but you are doing it for survival, you slowly begin to believe that this is the correct thing and you make sure everybody else does it. Otherwise the world should have changed by now. So this idea of saying I do it because I can’t help it is actually not true.
HS: But, today, do you think it is even possible to come up with ways of judging huge numbers of applicants for jobs/fellowships/ PhD etc. without resorting to convenient metrics like H-index or number of publications?
RG: Absolutely. Why are you imagining that there are always hundreds of applicants? There are hundreds of applications sometimes, when we may be forced to use unsatisfactory metrics. But the tendency always is to think of one unlikely scenario where you have no choice but to do something, and, with that, hide all the hundreds of scenarios where we can do much better. We say how else can the president of a large university with 3000 faculty decide who is good. Why should he decide who is good? He should not. He should depend on many others. If I have to judge people I will read the papers of those whose work I understand. For those whose work I don’t understand, I will get the help of trusted colleagues who understand. There will be at least one person in this world who will be able to read and judge another person. And even if there is nobody, then you take that candidate anyway – he must be good if there is nobody in the world who can judge him. So we don’t have to imagine extreme situations all the time
There was a time, 20 years ago, when I used to spend some days in selection committees for choosing people for one thing or another, a prize, a fellowship, a job. In each such committee somebody would come and give us a very nice description of the work of the applicants/nominees before we made our decision – these were really like a series of mini-seminars on a wide range of topics. It was a most interesting and most satisfying experience. But now, in the same selection committees, everybody comes and talks only about the number of publications, citations and H-index. I hear this for hours or days and I’m bored to death. We just don’t seem to read anymore. This is a fact of life. Because these metrics are available, we have stopped reading. It’s absurd. The world in which we live is completely absurd. And I think we are not realizing it.
HS: So when you find yourself in a position where you have to judge the work of your peers or students, what do you look for?
RG: If the judgement is to be based on reading, then I read. And when I don’t understand I ask. I ask other people to read and explain to me. I do not judge on numbers of papers or citations or impact factors. I judge on the content and I try to understand the content and I try to compare the content. That’s baseline for me. I am really impressed by a piece of work if I feel: Why didn’t I think of it? That’s my ultimate test. Lot of things are boring. Anybody can do it. If I had to pick one out of 10 people then I would apply that criteria. In addition, I would say: What would have happened if this paper was not published? Would it have made a difference to the field? You can always say all data is necessary, and, in the future who knows somebody may need it. Fine, but suppose I want to give a prize to one out of 10 people, I would certainly apply this kind of criteria. What would have happened if this paper had not been published? Would the field have changed? Would the field have slowed down? And do I feel that I wish I had done this piece of work? Now if you say that my method is subjective, of course it is. That is why we should keep changing committees frequently so that all manner of subjective assessments by diverse sets of people will even it out.
HS: What about a piece of work makes you feel: why didn’t I think of that? Does it depend on how novel the work is, does it depend on risk-taking, does it depend on being correct?
RG: It definitely doesn’t depend on being correct. It is cleverness. There is a clever way to do things and there are dull ways to do things. For example, let’s say you take a well-known technique in one field and apply it to another field in an extremely exciting way. If you apply it in the same field there is nothing so great about it. Sometimes when I see work which is highly-valued or published in Nature, I ask myself: why did this person and not that person do this? Often the answer is: Because only this person had access to this data, or this population, or that instrument. That is not so great. It’s not surprising that they did it. I am excited by work that anybody could have done, in principle, but only one person did it. That’s the kind of work that makes me think: why didn’t I think of that?
HS: Could you name a few pieces of work or scientists whose work provokes that reaction in you?
RG: I could probably do it, but I prefer to give you a slightly different answer to the same question. This is something I have thought through and written about. When I was an undergrad. I was absolutely fascinated both with animal behaviour and molecular biology and I used to read everything I could get my hands on, on both of these subjects. But I had a very different reaction to what I read. When I read in molecular biology, it was absolutely fascinating, and I’ve described it as a play being played on a stage in heaven. It was all wonderful but I never felt jealous because, as an undergrad student, the thought never crossed my mind that I could have done those things. But whenever I read a paper in animal behaviour, in addition to feeling awe, I felt jealous. I felt why didn’t I do this; it’s something I could have done. That is the difference in my reaction to these two kinds of things. I couldn’t have discovered DNA Polymerase as an undergraduate, but I could have discovered imprinting. So it certainly depends on what I can do and what I cannot do. If it’s something that anybody can do, and you do it, that’s great. If only you could do it, and you did it, then well it’s okay.
HS: Can you give us some specific examples of work, like imprinting, that impressed you?
RG: There I have this whole set – I have written about it – of examples from both fields. Let me give you a recent example to emphasize that correctness is not important. When Hamilton came up with his idea of inclusive fitness, he realized, and only he realized, that because of haplo-diploidy, it’s easier for Hamilton’s rule to be satisfied in Hymenoptera than any other group of animals, because the relatedness between true sisters is 0.75. This was a major breakthrough because 11 out of 12 independent origins of eusociality had happened in the order Hymenoptera, which represents only 2% of the animal kingdom. In the remaining 98%, it happened once (in termites). In those days that’s all that was known: 9 or 10 times it happened in 2% of the animals and once in the remaining 98% and it is the former group that was predisposed to eusociality because sisters were related by 0.75. It turned out to be wrong in the end but that is completely irrelevant. To me this was a creative leap. And I wished I had thought of it. Even today, even though I have been partly responsible for proving that it is wrong, I still feel I wish I had thought of it. The original formula of what we now call Hamilton’s rule was creative on its own but it was even more creative to realize that in haplo-diploidy it works much more easily. Or take Trivers’s work. Just the whole idea of parent-offspring conflict is such an elegant, such a beautiful, idea. Anybody should have thought of it, especially after Hamilton’s ‘64 paper. But between ‘64 and ‘72 nobody thought of it. If you just look at the idea, it is so creative. Why there would be a zone where both parent and offspring would agree that more investment should go to offspring, and then there would be a period when they disagree, and then there will be a period when both will agree that no more investment is appropriate. I wish I had thought of it. If I think hard I can also come up with experimental strategies or designs that I consider creative – Von Frisch’s experiment, for example, where he came up with the so called fan experiment. He wanted to prove that honeybees actually got information about the direction from the dance of the scout bees. So in his experiment he trained bees to take sugar from a particular feeder at a particular angle say, 250 m from the hive. To test their knowledge, he put not one test feeder but an array of test feeders, and he didn’t put them at 250 metres, but at 200 metres. Now these two are strokes of genius. He didn’t put them at 250 but nearer because he wanted to rule out the possibility that, at 250, the original bee had left some scent. And then by having the array rather than a single test feeder, he realised that, of course, they would make error, but the error should be symmetrical on both sides, and they should fall off, and the maximum should be in the middle, and then there should be a symmetrical fall off on both sides. That’s exactly what he found. Absolutely brilliant.
Or even the very very simple primitive experiment that Tinbergen did to show that landmarks are being used by digger wasps to recognize their nests in the ground. Again, when something is quick and dirty it is even more charming. Tinbergen worked in this place where the wasps kept making holes in the ground and raised their brood there and he saw that the holes all look the same but each wasp went only to its hole. How do they manage that? He said maybe the wasps have a detailed knowledge of the landmarks around their nest. Now how would you test this idea? Today we might take very detailed photographs and use pattern recognition software and say the grass here is a little shorter and a little taller there. We can get the computer to map the exact landscape etc. But Tinbergen didn’t do any of that. He reasoned that if they are using landmarks and the landmark differences are very subtle, he can exaggerate the differences. There were lots of dead pine cones lying around and so he put an array of pine cones around the nest and let the wasp fly in and out and learn it a little bit. Then he removed those pine cones and put them a little bit away and reasoned that if pine cones is what it has learnt it should go to the new place without the nest and not to the original nest now devoid of pine cones. And sure enough that’s what the wasp did. Then he asked whether they see the pine cones or do they smell them? He now dipped the pine cones in alcohol to remove whatever smell they may have and put them back. Nevertheless the wasps still went to where the pine cones were, suggesting that they are not using smell.
In another experiment von Frisch wanted to see if bees had colour vision, so he showed that they could distinguish between blue and green. But then you could distinguish blue and green because they may appear as two shades of grey. How do you remove that possibility? What did von Frish do – he goes to an art shop and says give me every shade of grey paper you have. He gives all alternatives of grey and says the bee must be confused by at least one of the shades of grey, if it is learning to distinguish between two colours as shades of grey. The bees did not confuse the colours with any shade of grey. I would give that piece of work the prize and not for somebody who went into the brain and recorded everything and showed that they had the right neurons to have colour vision. All that is okay if you can afford it but what von Frisch did was the work of a genius.
HS: How do you encourage and increase creativity in your lab?
RG: One of the easy ways to do this, which we do all the time, is we discuss other people’s work. I promote this idea of appreciating something not because it is sophisticated, not because it’s published in Nature, not because it’s correct, but because it is very original and creative. So you can promote this philosophy by constantly judging other peoples work and then injecting this philosophy while making those judgements. The harder job is to actually get students to become creative themselves. If you are the supervisor, then on the rare occasion when two students come up with two different ideas you can say why you like one or the other based on these criteria. Although that doesn’t happen every day. In short, there is no better way than to lead by example – be creative yourself, but that of course is harder still!
A shorter version of this interview is available here: https://indiabioscience.org/columns/conversations/standing-conventional-wisdom-on-its-head
In a 2006 paper in Science, Peter and Rosemary Grant provided evidence that demonstrated a character displacement event in a Galapagos finch species. This was, probably, the first such documentation of character displacement in the wild. Ten years after the paper was published, I spoke to Peter and Rosemary Grant about the making of this study, and how this work has progressed since then.
(Interview conducted over email between 9th September 2016 and 30th November 2016)
Citation: Grant, P. R., & Grant, B. R. (2006). Evolution of character displacement in Darwin’s finches. Science, 313(5784), 224-226.
Hari Sridhar: The motivation for this paper was the character displacement event you observed in Geospiza fortis in 2004-2005, what you call “the strongest evolutionary change seen in the 33 years of the study”. What has happened in the next 10 years (2006-2016), in this character displacement story? If you were to extend the x-axis of Figures 2 and 3 to 2016, what would they look like?
Peter Grant & Rosemary Grant: No change from 2005 to the end of the study in 2012: a straight horizontal line on the graph of time.
HS: Is “no change” the case for the population graph (Fig. 3) as well? Does this continue to be the “strongest evolutionary change” you have detected so far in this system?
PG & RG: Regarding Fig. 3, numbers of both species rebounded after the drought, fortis more than magnirostris. Because there was no further change in the fortis trajectory, there was no more strong selection; so the 2004-06 episode of selection plus evolution remained the strongest in 40 years. Incidentally, if you have access to our most recent book you will see the full 40 years of morphological data (P. R. Grant & B. R. Grant 2014. 40 Years of Evolution. Darwin’s Finches on Daphne Major Island. Princeton University Press, Princeton, NJ). 2012 was the last year of the field study.
HS: What was the spark that ignited the idea for this work and this paper? Were you looking out for it right from the time G. magnirostris established a breeding population on Daphne in 1982? Or was it initiated by the dramatic character displacement observed in 2004?
PG & RG: To answer this question, we have to go back to the early 1970s for the origin of interest in this subject. At that time, I (PG) reviewed the evidence for ecological character displacement and found it to be generally weak. Certainly, patterns of variation in nature could be interpreted as the product of competitive interactions between species, but the problem was that each of the patterns could be explained in alternative, non-competitive ways. One of the motivations of our initial work in the Galápagos was the desire to do better. In his 1947 monograph on Darwin’s Finches, David Lack had pointed out some apparently clear-cut patterns. For example, on the small island of Daphne Major, the medium ground finch (Geospiza fortis) was smaller than elsewhere, and because the small ground finch (G. fuliginosa) was absent from the island, Lack argued that the medium ground finch had taken over the niche of the missing species. On other, larger, islands both species were present and morphologically very distinct. Since Daphne had probably been colonized from nearby, larger and older Santa Cruz, this seemed like an example of the opposite side of the character displacement coin – character release as it has been called. Thus, part of the research we began in 1973 was designed to test the hypothesis of character or competitive release. Then, about a decade later, Daphne was colonized by the large ground finch (G. magnirostris). When it became clear this was not an ephemeral event, and that large ground finches were more efficient at exploiting the large and hard seeds of Tribulus cistoides than the large members of the medium ground finch population, we started to wonder if, one day, large ground finches could have a competitive influence on medium ground finches. This did indeed happen, twenty-two years after the initial colonization.
HS: Please tell us a little about the actual writing of this paper. At what point in the process did you start writing the paper and when and where did you do most of the writing? Did this paper have a relatively smooth ride through peer-review and was Science the first journal you submitted this to?
PG & RG: It did not take us long to convert the data into a paper, because the results of all analyses were clear and interpretable. We started analysing and writing when staying with our daughter and family in Corvallis, Oregon, and finished it in Princeton. We held back from publishing until we had been able to return to the field in 2006 to check whether the next generation of fortis remained, like their parents, displaced morphologically (see Fig. 2) from the pre-drought position. They had. So we finished the paper and submitted it to Nature. The editor rejected it without review because of “insufficient interest to researchers in a broad range of other disciplines”. Therefore we promptly reformatted the manuscript and submitted it to Science. Here it had a completely different reception. The manuscript was sent out for review, and all three reviewers plus editor were highly enthusiastic about it. The paper was accepted with some minor changes at the end of May and published six weeks later. Almost exactly 10 years later Science published our follow-up paper, where we provided a genomic understanding of what happened during the character displacement episode. But that is another story, and we will be happy to share it if you wish.
HS: Yes, please do tell us more about the follow-up genomics work, and if it was also followed up in any other ways.
PG & RG: We continued the fieldwork for seven more years after the character displacement event, to determine the long-term outcome of introgressive hybridization, and to follow the fate of the new lineage we had discovered. We will be glad to discuss this later. 2012 was the last year of fieldwork. Even before then we had started to synthesize the long-term research in order to write a book about the Daphne study. The book was published in 2014 by Princeton University Press (40 Years of Evolution. Darwin’s Finches on Daphne Major Island).
The genomic work began with a small problem of trying to understand the genetic basis of a beak colour polymorphism in finch nestlings. Beaks are yellow or pink. In 2010, we discovered a paper had been written about the same kind of colour polymorphism in chickens. It was by Leif Andersson’s group at Uppsala. We were put in touch with Leif by a mutual friend – Phil Hedrick at Arizona State University. That was the start of our collaboration. We found strong evidence of a simple mutation that accounted for the polymorphism in most populations of finches. One thing led to another, and we shifted the focus to the larger questions of finch genome variation and evolution. This work has led to two major papers so far. First, we published a paper in Nature that used genomic data to reconstruct the phylogeny. We also reported discovery of a gene, ALX1, which is a transcription factor affecting the development of beak shape. A mutation in the same gene in humans gives rise to cleft palate. Second, we published a paper in Science this year on the genomic follow-up to the character displacement paper a decade earlier. In the new paper, we reported the discovery of another gene influencing beak development through transcriptional activity. This is HMGA2, and it comes in two forms in finches. One is present in species with large beaks and the other is present in species with small beaks. These two variants are correlated with beak size among members of the Daphne population of fortis, with heterozygotes being intermediate in average beak size as expected. We found that genotypes associated with large beak size were at a strong selective disadvantage in the drought of 2003-04. The selection coefficient, 0.59, is exceptionally strong for natural selection on a continuously varying trait in a natural population. In fact, variation in haplotypes statistically explained approximately one third of the variation in the shift in average beak size. So, although many genes govern beak size, as we know from heritability estimates, we had discovered a single gene with a major effect on beak size, and it played a large role in character displacement. Interestingly, beak shape did not change during the character displacement episode, nor did the frequency of ALX1 haplotypes.
HS: Please tell us a little more about the work you did to determine the outcome of introgressive hybridization and the fate of the new lineage.
PG & RG: At the beginning of 2005, fortis were smaller on average than at any time in the preceding 32 years, and the question was whether they would stay that way or gradually change back to their pre-drought size, as happened after the drought of 1977. Offspring of the survivors of the 2004 drought were, on average, almost the same size as their parents, as we expected from the very high heritability of body size and beak dimensions. And in fact, average body size and beak size remained small right up to the end of our field study in 2012. Therefore, character displacement was not ephemeral: it persisted for seven years.
Part of the reason for a lack of change after 2005 is introgressive hybridization. G. fortis receives genes from fuliginosa, a smaller species, and scandens, a larger species. Genetic inputs from these two sources appear to have been roughly equal and hence contributed to the maintenance of the status quo.
Another part of the reason for lack of change is the flourishing of the Big Bird lineage after the character displacement event. We should first explain what the lineage is and how it formed. The lineage was initiated by a particularly large finch (hence the name Big Bird) that arrived on Daphne Major Island in 1981. Microsatellite DNA data suggested it was a fortis x scandens hybrid that had immigrated from nearby Santa Cruz Island. It bred with fortis, and two generations were produced before the drought of 2003-04. Two members of the lineage, a brother and a sister, survived the drought and bred with each other in 2005, as well as in the following years. Remarkably, their offspring bred with each other or with their parents, so did the grand-offspring. In breeding entirely endogamously the lineage behaved like a new species.
Big Birds occupy the morphological gap between magnirostris and fortis. The gap widened as a result of character displacement in fortis, and thus the Big Birds were less constrained by potential competition for large seeds from large members of the fortis population. The Big Birds have flourished because their diet in the dry season is varied, encompassing the large seeds eaten by magnirostris, the small seeds eaten by fortis, and nectar, pollen and seeds of Opuntia cactus eaten by both of them as well as by scandens, the cactus finch. The Big Birds are thus a central generalist in the Daphne community of finches.
We have recently taken the eco-morphological study into the realm of genomics by collaborating with Leif Andersson and his molecular genetics group in Uppsala, Sweden. The goal has been to investigate character displacement as a genetic phenomenon. The group discovered two genes that influence the development of beak traits through transcription factors. One of them, ALX1, affects beak shape. The other, HMGA2, affects beak size. Each gene comes in two forms: two haplotypes. In the character displacement event, the haplotype of HMGA2 that is associated with large beaks was at a strong selective disadvantage and declined in frequency. This demonstrates at genetic level what we had previously shown at phenotypic level. Interestingly fortis receives ALX1 and HMGA2 haplotypes from both fuliginosa and scandens. The HMGA2 haplotype from fuliginosa appears to have enhanced the evolutionary response in 2005 to natural selection in 2004.
To conclude, the community of finches on Daphne Major Island has changed from a 2-species community to a 4-species community. The character displacement episode played a pivotal role in the ecological adjustment of one species to another. It was caused by one of the additional species (magnirostris) and apparently facilitated the expansion of the other addition (Big Birds). The frequency of an important gene affecting beak size underwent a strong change. Introgressive hybridization with fuliginosa and scandens contributed to the evolution of fortis. We are currently using genomics to gain a deeper understanding of the consequences of introgression and the success of the Big Bird lineage.
HS: How was the paper received, both within academia and in the popular press, when it was published? Did it attract a lot of attention?
PG & RG: The paper was received very favourably in the scientific literature, and that has continued in both scientific papers and in books. We cannot recall any attention given to it in the popular press.
HS: In concluding your paper, you say “Replicated experiments with suitable organisms are needed to demonstrate definitively the causal role of competition, not only as an ingredient of natural selection of resource-exploiting traits but as a factor in their evolution. Our findings should prove useful in designing realistic experiments, by identifying ecological context (high densities at the start of an environmental stress) and by estimating the magnitude of natural selection.” Today, 10 years after this paper was published, could you reflect on whether and to what extent this has happened?
PG & RG: The adjustment species make when brought into competitive conflict is still studied mainly opportunistically and observationally, not experimentally, by researchers alert to the possibility of character displacement. Three years ago, Yoel Stuart and Jonathan Losos reviewed more than one hundred reported cases of ecological character displacement. By applying strict criteria to the evidence, they concluded that only six cases (including Darwin’s finches) passed their test. Given so few examples documented in nature, it should be no surprise that experimental tests of the role of competition in character displacement in nature have not been done. The closest to our proposal was a study of sticklebacks in the laboratory by Dolph Schluter (1994). Microcosms have been investigated experimentally in the laboratory where conditions are strictly controlled and feasible mechanisms demonstrated. However, they do not address the question of applicability to processes in nature, or whether the results can be scaled up from micro- to macro-organisms and environments. Perhaps the best system for research in the field would be annual plants that have recently come into contact and shown evidence of competitive interaction. A promising environment might be alpine or subalpine habitat, where species ranges are shifting under climate change and previously separated species are now encountering each other.
HS: Today, in retrospect, is there anything that you wish you had done differently, or any other data you wish you had collected, at the time of the character displacement event in 2006?
PG & RG: It would have helped if we had quantified the seed supply before, during, and after the character displacement event by random sampling, just as we had done in every year from 1976 to 1991. However, given our observations, on the difficulty finches experienced in finding Tribulus fruits during the 2003-04 drought, we are quite confident that sampling data would have revealed a very strong decline in availability.
HS: In the paper, you acknowledge “K.T. Grant, L.F. Keller, K. Petren and U. Reyer” for fieldwork help. Could you tell us a little more about who these people were and how they helped?
PG & RG: K.T. Grant is our daughter, Thalia. She helped us with fieldwork in many years, beginning in 1973 when she was six years old. Her help was crucial in 2005, when she visited Daphne to census the banded finches in order to find out which ones had survived and which ones had not. Rosemary and I could not visit the island that year because I had to have an operation for colon cancer, followed by a three-month course of chemotherapy under a doctor’s supervision. Thalia’s visit to the island was then followed by a longer visit by the other three helpers. Lukas Keller (University of Zürich) and Ken Petren (University of Cincinnati) had been post-doctoral fellows with me, and Uli Reyer was head of the Ecology Department at the University of Zürich, host on our two long visits to his Department, and a good friend. Their visit was nicely timed, fortunately, as heavy rain fell while they were there. Therefore we know the exact date when the drought ended. As it turned out, Thalia had found almost all the survivors on her short visit, and although our other helpers added very few to the list, their inventory gave us more confidence in our estimate of the true survival. In the next field season in 2006 we did not find a single banded finch that had escaped detection in 2005.
HS: Have you ever read this paper after it was published?
PG & RG: No, we have never read it, we have only checked some numbers in tables.
HS: Could you tell us why you decided to end fieldwork on this project in 2012?
PG & RG: We both retired from teaching at Princeton University in 2008. The last of our research money was spent in 2012, and after 40 years of fieldwork it seemed a good time to stop and the write a synthesis, which became the book Rosemary and I published in 2014: “40 Years of Evolution. Darwin’s Finches on Daphne Major Island.”
In a paper published in Animal Behaviour in 1977, John Krebs, Jonathan Erichsen, Michael Webber and Eric Charnov showed experimentally that whether great tits (Parus major) are selective or not about prey choice depends only on the supply rate of the more profitable prey, and not of the less profitable prey. These findings partially supported a model of optimal foraging that they had developed. Twenty-four years after the paper was published, I spoke to John Krebs about the making of this study and what we have learnt since then about foraging decisions of great tits.
(Questions sent by email on 10 August 2016; responses received on 10 August 2016)
Citation: Krebs, J. R., Erichsen, J. T., Webber, M. I., & Charnov, E. L. (1977). Optimal prey selection in the great tit (Parus major). Animal Behaviour, 25, 30-38.
Hari Sridhar: What was your motivation to do the experiments presented in this paper?
John Krebs: To test a model of optimal prey selection
HS: This paper has four authors. Could you tell us how this group came together and what each member of the group contributed to this study?
JK: Erichsen designed the apparatus, Charnov did the modelling, Webber and I ran the experiments and the analyses.
HS: Who were the two observers – one who replenished the food and the other who watched the video monitor – during this experiment?
JK: Sometimes Krebs and Webber, and sometimes Krebs and Erichsen.
HS: How did you come up with the idea of using a conveyor belt apparatus for this experiment? Would you know whether the apparatus that you used still exists?
JK: Erichsen had designed the apparatus for another purpose. I doubt that it still exists
HS: Where and by whom were the four great tits caught? How did you find the fifth bird, which was raised from an age of 12 days?
JK: They were caught by Krebs at Wytham Woods, the fifth was hand raised by Krebs.
HS: Could you share with us what the codes ‘bw’, ‘gbw’, ‘ro’, ‘yy’ and ‘pw’ stand for?
JK: Colour ring codes: blue, white, green, red, orange, yellow, pink
HS: During the writing of this paper, how did the authors share, discuss and edit drafts of the manuscript? Would you remember how long the writing took?
JK: Don’t know how long it. Krebs wrote the draft and others commented
HS: Did this paper have a relatively easy ride through peer-review? Was Animal Behaviour the first journal you submitted this to?
JK: We didn’t submit it elsewhere. I don’t recall how the referees commented on it
HS: Were these results considered controversial soon after they were published? Did this paper receive a lot of attention from peers?
JK: The results weren’t controversial. The paper was, I think, well-received.
HS: Did this paper play a role in influencing the future course of your research career?
JK: It was one of our early papers on foraging theory, which formed a major research focus of my group for the following decade.
HS: Today, 39 years after it was published, would you say that the main conclusions of this study still hold true?
JK: I have no reason to doubt the results, but Rechten et al. 1981 Anim. Behav. 29, 1276-77 corrected the theory, and Berec et al. 2003 Can. J. Zool. 81, 780 were unable to repeat the results in toto.
HS: If you were to redo these experiments today would you do them differently?
HS: In the paper you say “it will be impossible to distinguish between ‘mistakes’ and ‘deliberate sampling’ until we have devised a specific predictive sampling model”. Was such a model developed subsequent to this paper?
HS: You say that “our failure to find this [a step change from no selection to selection for profitable prey] in our experiment is likely to be a general result”. Was this statement borne out by future research?
HS: In the 39 years since it was published, have you ever had to go back and read this paper for any reason?
JK: I did in the early days but not recently
HS: Among all the papers you have published, is this one of your favourites? If yes, why?
JK: It was one of our early papers testing optimal foraging models. In hindsight the theory and experiments could have been improved
HS: What would you say to a student about to read this paper today? What should he or she take away from this paper written 39 years ago?
JK: I would say it is a good example of how to link theory and experiment, but also that by today’s standards it is not a very sophisticated piece of work and much has been done since then to develop both the theory and experimental techniques.
In a paper published in Science in 1999, Andrew Hector and a team of collaborators reported the results of an experiment, replicated in eight European field sites, that showed that loss of plant species diversity leads to reduced above-ground plant biomass. Seventeen years after the paper was published, I spoke to Andrew Hector about the making of this project and what we have learnt since about the diversity-productivity relationship.
(Questions sent by email on 30 July 2016; responses received on 18 September 2016)
Citation: Hector, A., B. Schmid, C. Beierkuhnlein, M. C. Caldeira, M. Diemer, P. G. Dimitrakopoulos, J. A. Finn et al. 1999. Plant diversity and productivity experiments in European grasslands. Science 286: 1123-1127
Hari Sridhar: Please tell us a little about the motivation for setting up this multi-country experiment. Whose idea was it? Was it setup specifically to investigate niche complementarity and sampling effects?
Andrew Hector: Research on the link between biodiversity and ecosystem functioning only coalesced as a field following a conference in the early 90’s put together by Detlef Schulze and Hal Mooney. That meeting spawned several studies. Interestingly, the link between diversity and function can be traced all the way back to Darwin, but there was only sporadic study of it until the 90s. The multi-country approach of BIODEPTH was facilitated by the European Framework 4 – we had about a dozen groups in 8 countries led by John Lawton at the NERC Centre for Population Biology at Imperial College Silwood Park.
HS: You joined the BIODEPTH project soon after you completed your PhD. Can you share with us how you got into this project?
AH: Luckily, I spent much of the previous year working for Mick Crawley at Imperial College, monitoring on-going experiments and helping set up new ones, to earn money while I wrote my PhD up. That put me in a good position when the postdoc. came up for BIODEPTH.
HS: Please give us a sense of how this collaboration worked. How did people join this group? Did all of you meet anytime during the making of this study? Did you have regular online meetings?
AH: BIODEPTH was a success because of the great collaborative spirit – it was a real team effort and everyone in it made an important contribution to its success. The Framework 4 structure had meetings every 6 months and we worked our way around most of the sites.
HS: How did the writing of this paper happen? Did you do most of the writing? How were drafts shared and commented upon?
AH: The paper was born at one of the regular meetings. It was hard to explain to people how to send the data in for inclusion in the database so we went through the whole process in a mock example and then did a basic statistical analysis there and then. Seeing how quickly it could be done really motivated people to get the data sent in speedily.
HS: Did this paper have a smooth ride through peer-review? Was Science the first place you submitted this to? In what ways did the published version differ from the first submitted draft?
AH: Yes and no. Science were happy to have it but it had mixed reviews – some scientists were (and still are) quite against the whole idea that diversity can be important for functioning. To some degree, the final paper was a compromise between opposing reviewer opinions.
HS: In the Acknowledgements you thank “P. Heads and E.Bazeley-White” – can you tell us how these people helped? You also thank J. Nelder for advice on statistical analyses” – can you tell us more about this?
AH: Phil Heads managed the NERC Centre for Population Biology for John (he was one of his ex-PhD students) and Ellen managed the database (she is now at British Antarctic Survey). It was great to have both of them to help support the work. John Nelder was a very influential statistician. We hired him to hold a short workshop where we could bounce ideas for the analysis off him.
HS: You say you used “standardized protocols to establish experimental assemblages “. Can you tell us a little more about these protocols?
AH: The details are too technical to go into here. The key point was that each team followed the same approach at the different field-sites to make the data as comparable as possible.
HS: Did this paper attract a lot of attention – in academia and in the media – when it was published?
AH: Yes. Interestingly, the media did not find the idea controversial – it seems to make sense to people that biodiversity affects how ecosystems work – but some scientists did.
HS: What impact did this paper have on your career and the future course of your research?
AH: Obviously getting my second publication into Science was a huge break – I was very lucky to have had the opportunity.
HS: It is now 17 years since this paper was published – would you say that the main conclusions from this study still hold true?
AH: Yes, in general. We have realized many scientific results are not reproducible (‘the reproducibility crisis’) but the BIODEPTH results turned out to be very reproducible despite being controversial with some people. The experiment has been repeated in the US (Cedar Creek), Germany (Jena), the Netherlands and elsewhere and all results fall in the range seen in our study.
HS: If you were to redo these experiments today, would you do anything differently, given the advances in technology, theory and analytical techniques?
AH: We tried to manipulate both species richness and functional groups and although their effects cannot be totally separated (more groups means more species) it would have been nice to have teased them apart a bit more (although the experiment in the Netherlands did this for legumes, omitting them from their study). We used random mixtures of species due to some practical constraints. It might have been nice to use mixtures that reflected how species might be lost in reality, but this is hard to predict and depends on what is driving species loss. And, on the other hand, randomization is a key feature of good experimental design and a good place to begin.
HS: In the paper you say that this was “the most extensive experiment to date in terrestrial ecosystems.” Since then, have there been bigger experiments on this topic?
AH: At single sites yes (Cedar Creek and Jena), and BIODEPTH seems to have been partly responsible for the current popularity of networks (coordinated distributed networks) like Nutrient Network and Drought-Net.
HS: Did the work presented in this paper serve as a motivation for Loreau & Hector 2001?
AH: Yes. Basically we had a pattern, but could not pin down the mechanism. The 2001 paper helped us to do this.
HS: In your paper you say that “There may also be transient effects at this early stage of the experiment that largely disappear by the following year”. Can you tell us whether this has happened in subsequent sampling?
AH: Sadly, the EU framework 4 only allowed us to keep the 8 sites going for 3-4 years (some ran for longer) but longer term work at Cedar Creek and Jena has shown the effects generally get stronger over time as the experiments go on.
HS: At the time of this study, Trifolium pratense was the only species that had particularly marked effects on productivity. Since then have other important species been discovered?
AH: Actually, that result has to be taken in the context that red clover was one of the few species grown at all sites. I don’t doubt it has strong effects (it is a nitrogen fixer) but the design could not get at the effects of all species.
HS: What is the status of the plots used in this study? Do they continue to be used for these experiments? Have the sites in which these plots are located undergone any changes since the time of this paper?
AH: As I said above, sadly we could not keep the study going in the long term but the projects at Cedar Creek and Jena are still going.
HS: At the time you did this study, did you anticipate that it would be cited so much? Do you know what this paper has been mostly cited for?
AH: I didn’t really think about it but it was a new field and a controversial topic so it is not surprising. It is cited as evidence that biodiversity affects how ecosystems function.
HS: Have you ever read the paper after it was published? When you read it now, what strikes you the most about it?
AH: Not recently. I remember there is a mistake in it – at one point we say species richness affected diversity (when we meant productivity).
HS: What would you say to a student about to read this paper today? What should he or she take-away from it?
AH: That it is important to repeat the same study to see how repeatable or variable the result it.
HS: Is this your favourite paper among all the papers you have published? If yes, why? If no, and if you do have another favourite, which is it and why?
AH: It seems a long time ago now (it was!) but obviously it will always be one I remember. My other current favourites are:
In a paper published in Nature in 1982, Malte Andersson showed, experimentally, that female long-tailed widowbirds choose mates based on the lengths of their tails. Andersson’s study was, arguably, the first experimental support for Darwin’s Sexual Selection theory. Thirty-four years after the paper was published, I spoke to Malte Andersson about the making of this study and what we have learnt since about mate choice in widowbirds.
(Questions sent by email on 7 July 2016; responses received on 17 September 2016)
Citation: Andersson, M. (1982). Female choice selects for extreme tail length in a widowbird. Nature 299: 818-820.
Hari Sridhar: What was your motivation for doing this study ? How and when did you first come to know about long-tailed widowbirds?
Malte Andersson: My interest in sexual selection and signaling was seeded around 1970, during my doctoral studies of behaviour and ecology of long-tailed skuas in Lapland, Northern Sweden. The long-tailed skua is a relative of auks and gulls, and turns rodent predator in the far North during the breeding season. Inspired by the comparative ethological studies of gulls by Niko Tinbergen’s group, my aim was to study skua behaviour and its adaptations to an ecological lifestyle very different from that of its phylogenetic relatives. I was aware that both sexes in skuas have a pair of elongated central tail feathers that differ markedly in shape and length among the four Northern hemisphere species. In the field, I found that both sexes raise and expose the tail conspicuously during courtship, and I wondered about its function. Perhaps the elongated feathers are important for species recognition in pair formation? But at their breeding grounds, the species are easy to tell apart for a human observer, based on size, calls, coloration and other aspects. So why should the birds need different tail shapes for that purpose? Species recognition did not seem an entirely plausible hypothesis. On the other hand, catching the same individuals over several years, I found that the central tail feathers became longer and therefore reflected age and perhaps also survivorship. I wondered if that might somehow be relevant.
About a decade earlier, Peter O’Donald, Ronald Fisher’s last doctoral student, had studied sexual selection of color morphs in Arctic skuas. Reading his pioneering papers made me aware of Darwin’s and Fisher’s theory of sexual selection by female choice. I also read widely outside the curriculum, visiting our university library each weak, skimming journals in behavior, ecology and evolution for interesting new studies. I was also influenced by books on evolution, selection and adaptation by George Williams, John Maynard Smith and John Merritt Emlen, which strengthened my interest in evolution. After my dissertation, these research fields, in particular sexual selection, full of interesting theory and unsolved problems, were on my mind. During a visit to East Africa in 1975, I saw long-tailed and Jackson’s widowbirds on their savanna breeding grounds in the Kenyan highlands. Why were male long-tailed widowbirds, with their black plumage, red wing epaulet and, especially, a half meter long unwieldy tail, so different from the females, which resembled dull females of other weaverbirds (Ploceidae)?
HS: This is the first test of Darwin’s hypothesis about male sexual ornaments. Why do you think it took so long for it to be experimentally tested?
MA: Most biologists for a long period were skeptical about Darwin’s ideas on mate choice, and many remained skeptical even after the ‘evolutionary synthesis’ in the mid 1900’s (e.g. Huxley, Lack). And, in spite of early pioneering work by Niko Tinbergen, experimental tests of behavior in the wild gained momentum only in the 1970’s and 80’s. Then, new results made it increasingly clear that field experiments in the natural environment could often provide decisive results and distinguish between hypotheses in behavioral and evolutionary ecology, clarifying the function and adaptive significance of a trait. Controlled field experiments thereafter became more common.
HS: During this study, what was a typical day in field like?
MA: Usually going to the field site a while after sunrise, when widowbird males returned to their grassland territories from the night roost. We caught territorial males with a clap-net trap. Before and after catching and manipulating a male, I measured his display activity. After the sun dried out the morning dew from the tall grass, I searched for nests of females breeding in the territory, doing so once a week until the end of the breeding season.
HS: You started the fieldwork for this study in November 1981. In the same month, a conceptual paper on sexual selection you wrote was accepted in the Biological Journal of the Linnean Society. Did this paper, in some way, motivate your study on widowbirds?
MA: Yes, in a general way, as work on theoretical aspects of sexual selection made me read and think about debated issues of female choice and male ornaments. Fisherian runaway selection was one possibility, and it also seemed likely to me that ornaments could indicate phenotypic and genetic fitness, through resource allocation, as portrayed in a figure in the paper you mention. I thought that, in spite of lingering skepsis among many researchers, female choice based on male ornaments was plausible, encouraging me to attempt an experimental test.
HS: Did you do all the fieldwork on your own or did you have help in field?
MA: In catching the birds and during the experimental manipulations, a field assistant, first Uno Unger, then Kuria Mwaniki, helped me. He held the male in a suitable position, while I cut and glued the tail feathers. This way there was no need for anesthetics, and the bird could be released immediately after being manipulated and ringed.
HS: How difficult was it to find the nests?
MA: It was more time-consuming than difficult. Females build their rather large-domed grass nest in the upper third of 0.5 – 0.8 m tall grass in the male’s territory. Females usually flew from the nest when I was several meters away. By systematically searching the grass areas of the territory in parallel walks about 2 m apart, I located the nests, and I repeated the search each week until the end of the breeding season, when no new nests were started.
HS: Walk us through how you came up with the idea of modifying the tail lengths of these birds? Was it tricky to cut and paste the tail feathers back? Did you use a particular brand of glue for this?
MA: Controlled field experiments was an approach I had used in several earlier studies during work with skuas and lemmings in Lapland. And I was aware of the nice experimental tests of the function of red wing epaulets in red-winged blackbirds in USA. So, experimental testing of a conspicuous male ornament, potentially involved in female choice, was not a far-fetched approach. In fact, I had been thinking about this possibility for a long time, but then with the epitome of male ornaments in mind: the train of the peacock. I explored possibilities for doing such a field experiment during a visit to Sri Lanka in 1979, but found that such a study of peacocks in the wild would be difficult for several reasons. The lek sites I found in a national park were in jungle with plenty of elephants and wild buffalo around; not an ideal situation. In addition, manipulating trains of unwilling peacocks in the wild seemed to present some problems of its own. That made me think again about the African widowbirds, which appeared more manageable.
When I planned the experiments, rapidly hardening cyanoacrylate superglue was coming on the market. The brand I used was called “Hot Stuff”, from Satellite City Instant Glues. Testing with feathers from other birds, I found that the glue hardened quickly enough, in just a few seconds, to be suitable for use in the field for tail elongation. I practiced and improved my skill at feather manipulation at the lab before going to Kenya for the study. During manipulations in the field, the assistant sat in front of me holding the bird, while I cut, trimmed and glued the tail feathers.
HS: Fig. 1 in this paper is one of the nicest figures I have seen in a scientific paper. Whose idea was it to include the widowbird illustrations perched on the bars in the graph? How was this figure made at that time?
MA: I thought carefully about how to include, without overloading the figure, as much information as possible. For instance the number of nests for each individual male at the bottom of the bars. The idea of having perched widowbirds with relevant tail lengths on the bars came rather naturally, because this was the way I often saw males in the field. There were many cattle fences in the area, and fence poles were the favorite perch sites for territorial males. I made the first version of the figure, which was then redrawn in ink by a departmental lab assistant, Aino Falk Wahlström, skilled at illustration work.
HS: One of the unique aspects of your study is the elegant “double control” you used for the experiments. Was this the first time such a design was being used?
MA: I am not aware of any previous study with such a design, but it may well have been used before. I first planned to use only the color-ringed birds as control, but became worried that the cut-and-glue operation might have an important effect, so added a control for that.
HS: Your paper presents a lot of natural history information on the widowbird. Was this already known or did it come from your own observations?
MA: Some of it was known from earlier studies of the South and the East African subspecies (e.g. Craig 1980). Other aspects I learned during fieldwork.
HS: Today, do we know more about aspects of this bird’s ecology which weren’t well-known then, e.g. nest-site choice by females, role of tail length in competition, and territory ownership?
MA: There has apparently not been much more fieldwork on this species, but several other widowbirds have been studied extensively by observations, experiments and comparative phylogenetic analyses, in particular by my former PhD student Staffan Andersson (no relative!) and his research group.
HS: Today, do we know more about why females choose long-tailed males in this species?
MA: Our knowledge about mate choice in other widowbirds, and of course more generally, has increased vastly in the 34 years since the study was published, but there have been no further studies of mate choice in this species. The reason may be that a number of other widowbirds, whydas and other species also have long tails. Researchers have apparently preferred to study some of these other species rather than the one I already studied. Focusing on another species permits both another independent test of tail function, and can show if ornamental long tail plays a role in female choice more generally among birds. A number of studies of different species have found that it does.
HS: Your work was entirely experimental. Have there been studies looking at whether your findings hold true with respect to natural variation in males?
MA: Not in this species, but in many other birds, studies based on natural variation have found that male mating success correlates with ornament size.
HS: Did this paper create a buzz – within academia and outside – when it was published?
MA: Yes, it raised much interest among biologists, demonstrating sexual selection by mate choice of a conspicuous ornament, of the kind that long puzzled Darwin, until he arrived at the essentially correct explanation. It also raised interest in general news media, some of which reported that now it has been proved: the length matters.
HS: How important has this paper been in your career? Has it had a major influence on the course of your future research?
MA: It had a major influence. Sexual selection is a field full of both fascinating natural history and interesting debated theory. Partly as a consequence of the simultaneous publication of the widowbird study and my theoretical paper in Biological Journal of the Linnean Society, I was invited by editors at Princeton University Press to write a monograph about sexual selection. Not anticipating the eruption of coming studies I gladly accepted. That decision kept me busy for a number of years. When the first version of the book manuscript was finished, it was necessary to revise almost every chapter, because so many new important results had been presented in the meantime. And the same procedure had to be repeated again also when the revision was finished, until I could finally deliver a manuscript that was reasonably up to date with the latest findings. Writing the book greatly reduced my available time for widowbird work and other research. Fortunately Staffan Andersson, after presenting his thesis on Jackson’s widowbird, could continue comparative and experimental studies of sexual selection of coloration and other ornamental traits in widowbirds and bishops, which remains a successful ongoing project. After gaining more time for own research when the book was finished, I have worked for instance on various aspects of breeding systems.
HS: Have you ever gone back and read this paper after it was published? What aspects about it strike you now? What memories does it bring back?
MA: Yes, I have read the paper in preparing some talks and lectures. A nice aspect is its brevity. The experimental design, planned after a pilot visit to the study site a year before the experiment, made the outcome rather clear and easy to write about, resulting in a short informative paper. Reading it now recalls exciting fieldwork in a beautiful rural part of the Kenya highlands, with cool nights and hot sunny days, helpful and friendly Kikuyu farmers, and the Nyandarua Mountains as a magnificent backdrop under a clear sky. (There were thunderstorms and torrent rains too, but they seem to have thinned out in my memory.)
HS: If you compare this paper to papers you write today, do you find any striking differences, e.g. in writing style?
MA: Not that I am aware of. I try, but of course fail, to write as simply and briefly as possible, without sacrificing clarity and readability. A researcher that in my opinion wrote lucidly about quantitative evolutionary problems was John Maynard Smith. Authors with such writing style were for instance George Orwell and Kurt Vonnegut.
HS: Have you had the opportunity to go back to your study site after the paper was published? Has the site changed a lot since the time you worked there, in 1981-82?
MA: I have not been back since the mid-1980s, but even then, some of the breeding habitat of long-tailed widowbirds was disappearing, being turned into arable fields or plots for growing vegetables, and the nesting grass (Eleusinae) was being cut for thatching of roofs.
HS: This paper has been cited 793 times (Google scholar) as of today. Did you anticipate that it would generate so much interest? Do you know what your paper has mostly been cited for?
MA: I had no idea it would raise so much interest. It has probably been cited mostly because it experimentally demonstrated female choice based on a conspicuous male ornament in the wild.
HS: What would you tell a student who is about to read this paper today? Any caveats? What should he or she take-away from it?
MA: I spent much time thinking about the experimental design, and exploring the possibility for such a study by a pilot visit to the field site. So the importance of careful planning is probably a useful takeaway. Viewed today, there are many caveats. For instance, there is no paternity determination, as DNA methods were not then available. And the adaptive reasons for female choice of males with long tail could not be studied in this brief experiment. But the successful experimental demonstration of female choice in the wild may have helped encourage subsequent better studies.
HS: Among all the papers you have written, is this your favourite?
MA: Yes, I believe it is my best paper because it is short and informative, reporting a fairly clear outcome of a controlled, interesting experiment. It demonstrated, in the wild, female choice of mate based on a conspicuous ornament, one of Darwin’s most controversial ideas. Another often cited sexual selection paper is a model (Evolution 40:804-816) showing that a genetic indicator process of mate choice can work, taking to higher frequencies a female preference and a preferred male ornament that reflects genetic viability. This, together with similar results from other researchers, may have helped generate more interest and more sophisticated modeling and empirical testing of such processes in sexual selection.
In a paper published in Animal Behaviour in 1991, Marion Petrie, Tim Halliday and Carolyn Sanders showed, through an observational study, that: 1. mating success of male peacock was related to the number of spots on their tails; 2. the relation between mating success and number of tail spots was a result of female choice, i.e. females preferentially mated with males with a greater number of tail spots. Twenty-five years after the paper was published, I spoke to Marion Petrie about the making of this study and what we have learnt since about the tail of the peacock.
Questions sent via email on 1st July 2016; responses received on 21st September 2016
Petrie, M., Tim, H., & Carolyn, S. (1991). Peahens prefer peacocks with elaborate trains. Animal Behaviour, 41: 323-331.
Marion Petrie working at a peacock farm in Norfolk, UK (©Tom Pike)
Hari Sridhar: In the Introduction of your paper you cite only three references. One is Darwin. The other two are studies that manipulated a male character and measured mating success. What role did these studies play in motivating your work?
Marion Petrie: Although Darwin first suggested that the peacock’s train had evolved as a result of female choice, no one had tested this idea. I was working at Whipsnade Park on a study of Chinese Water Deer, and, whilst staying overnight in the park, noticed the free-ranging peacocks displaying in groups (lekking). I thought that it would be feasible to study the peacocks at Whipsnade (that it would be relatively easy to catch and mark them) and test Darwin’s hypothesis. The beauty of a lek mating system is that the process of active female choice is directly observable.
Lekking peacocks at rest in Flint Pit Paddock, Whipsnade Park (© Marion Petrie)
HS: This paper has three authors. How did this group come together and what was the contribution of each author? Who did most of the writing?
MP: Tim Halliday held a lectureship at the Open University, which was the closest University to Whipsnade Park, and had an interest in mate choice. I met Tim at a conference and talked about studying the peacocks at Whipsnade. We wrote a grant application to the Natural Environment Research Council (NERC) to start the study together. This grant included provision to appoint field assistants for the breeding season and Carolyn Sanders acted as my most excellent assistant on the project. The paper was written after the field season and Carolyn was not involved with writing. It is hard to recall exactly who wrote what, but looking through my files it looks like I produced a first draft which Tim then improved and added to. Tim is also a talented artist and drew all the lovely figures.
HS: What is the history of the “free-ranging, feral population of blue peafowl at Whipsnade Park”? When were peafowl brought there and what for?
MP: Whipsnade Park belongs to the Zoological Society of London, and I am afraid that I know very little about the history of the population of the peafowl, although it had been in existence for at least 40 years when I started working there. I know that peafowl born in captivity at London Zoo were brought to Whipsnade, and that Whipsnade provided a home for other peafowl from other sources. The keepers at Whipsnade sometimes caught and sold peacocks. So my impression was that there were movements in and out of the population, and that this had been going on for some time.
HS: Have you ever had the opportunity to observe peafowl in their natural range?
MP: I have been to India twice for short filming trips during the peafowl mating season, and had the opportunity to watch peafowl there, although they were not ringed. It was possible to observe a “lek” and courtship, and, although I didn’t see an actual mating, it was fairly easy to observe peacocks displaying close together in Sariska National Park. One of the aims of the filming trips was to film tigers and peafowl, so I also went to Ranthambore National Park. I can remember seeing peacocks in flight there…a fabulous sight! Although I didn’t note any obvious differences in behaviour between Indian and UK birds, there was an obvious phenotypic difference: the peacocks in India tended to have longer legs, and, as a result, held their trains further up from the ground.
HS: What was a typical day like when you were doing this work? Did you do the trapping and banding and lek observations yourself? Who was Nigella Hillgarth, who you acknowledge “for help in marking and measuring the birds”?
MP: I don’t think I can describe one typical day because they would vary so much over the year. But some tasks would predominate at particular times of the year. I was heavily involved in catching birds in the months prior to the breeding season, and took all the measurements myself, whilst Nigella held the birds (to make sure the same person took all the measurements). My memories of this was that it was very cold as we had a small unheated shed to work in, and under these adverse conditions, Nigella and I became great friends. Sometimes we had large numbers of birds to process all at once, so we would work very long hours. At the time, Nigella was a PhD student working on pheasants in the Zoology Department in Oxford, and Bill Hamilton was her supervisor. Nigella was interested in the ecto-parasites of peafowl, and as part of her work, we recorded the number of feather mites drinking at the eyes of the peafowl in a time period. Nigella and I are still in touch, and she is now the president and CEO of the New England Aquarium.
During the mating season, I was heavily involved in watching the birds. The lek watching started in mid-April and continued until the end of May; Tim and Carolyn also covered some of the watches. The aim was to arrive at the lek early in the morning, before peacocks left their roost sites, and continue until the males stopped displaying, around the middle of the day. This could mean very early starts for me, as I was living in Norfolk at the time, and it was a 100 mile drive to the Park. We would watch from a small canvas hide, sitting on a small canvas chair, but sometimes we had to kneel to move round the hide, in order to follow females moving between males situated around the hide. Watching the birds was extremely interesting and stimulating. There was always something new to see, and many observations would make you ask ‘why are they doing that’? Some observations would provoke analyses that contributed to a paper. An example of this was the observation that certain females would sit by particular males and engage them in courtship at times when another female tried to approach them.
After the mating season I was involved in data analysis and writing up, preparing to give talks at summer conferences, applying for grants and jobs! This went on until Christmas and then the cycle would begin again.
HS: The observations ended in May 1988 and the paper was submitted on 8 July 1989. Can you give us a sense of what happened in the intervening one year?
MP: Whilst the observational work ended in May 1988 for this paper, we were still working at Whipsnade. In April and May 1989, I had four field assistants and we watched at four leks within the park. After the end of the observation season in 1988 there was a period of analysis and writing the paper first for Nature and then for Animal Behaviour. The referees requested changes so the paper needed to be revised before it was eventually published in Animal Behaviour On a more personal note my second child was born on 1st August 1989.
HS: Was the term “hoot-dash” used for the first time in this paper? Is it still used when describing peafowl mating?
MP: No, hoot-dash was in the literature and is still used as far as I know.
Mid Hoot-dash, Flint Pit Paddock, Whipsnade Park (© Marion Petrie)
HS: Was the photo in Fig. 2 of the “hoot-dash” taken in Whipsnade park? Was Chris Pierpoint a professional photographer?
MP: Yes it was, and Chris was one of the four excellent field assistants working in 1989 and was a very good photographer.
HS: Did this paper have a smooth ride through the publication process? Was Animal Behaviour the first place you submitted it to?
MP: We first submitted the paper to Nature but it was rejected, so we rewrote the paper for Animal Behaviour. Nature has a very strict word limit, so the first draft of the paper for Nature was a lot less expansive than the Animal Behaviour version.
HS: You acknowledge Morris Gosling and Robert Gibson for “comments on an earlier draft”. Could you tell us who these people were and how you knew them?
MP: Morris Gosling and I worked together on Chinese Water Deer at Whipsnade and on lekking in Topi in Kenya. He is also my long-suffering husband. Robert Gibson is a colleague who has done some outstanding work on mate choice and lekking in sage grouse.
HS: How did the collaboration with Alan Grafen, for the female choice null model, come about?
MP: I gave a talk at the Zoology department in Oxford and presented the data on the sequence of males and females visited. Alan attended the talk, came up to me afterwards and kindly offered to analyse the data as it is now presented in the paper.
HS: You say “a large part of the variance in mating success can be attributed to train morphology and that females choose to mate with those males that have the most elaborate trains of those sampled”. You also say “Our data do not suggest that competition between males is an important determinant of mating success”. Today, 25 years after the paper was published, do these statements still hold true for peacock mating behaviour?
MP: I do think that there is good evidence for these statements from the data that we collected at that time. Whether it is ‘true’ for all peafowl everywhere is a different question, and whilst some studies have found the same positive relationship between train morphology and mating success, at least one Japanese study claims that no such relationship exists (although, they did find a non-significant positive correlation). Of course, if females do not prefer peacocks with elaborate trains it does raise the question of why the peacock’s train has evolved, and I haven’t seen any good data that support any alternative hypothesis.
HS: In the Discussion, you highlight many questions for future research – how females assess males, why do females choose males with more elaborate trains, what determines whether males obtain a display site, how do males choose leks – have these questions been addressed since?
MP: I do think we are further ahead with these questions: how females assess males has been looked at in a nice study where the researcher attached eye-trackers to peahens and showed that peahens do look at the train.
Why females choose males with more elaborate trains formed the basis of much of my future peacock work, after the publication of this paper. I removed peacocks from Whipsnade and bred from them in captivity. This was a controlled breeding experiment, where each Whipsnade cock was mated with 4 females, and the subsequent eggs removed from pens and artificially incubated and hatched in separate compartments, so we knew the sire for all the offspring produced. The young were reared in large groups and monitored regularly to record growth. When the offspring were old enough, they were released into Whipsnade Park and we observed their subsequent survival and future behavior. We found improved growth and survival of offspring of peacocks with more elaborate trains.
We also followed the male offspring of the release experiment through to sexual maturity and looked at where males started to display. We found that males would set up display sites close to their sibs or half sibs (even though they were not reared together). We also found from DNA fingerprinting that male leks in general consist of relatives.
Lekking males at rest in Whipsnade Park illustrating the extent of natural variation in both train length and number of train feathers (© Marion Petrie)
HS: Your study was entirely observational and with a small sample size (N = 10 males). Since this study, have you had the opportunity to repeat these tests with larger sample sizes and in an experimental way?
MP: Yes, I looked at the relationship between train elaboration and mating success in a much bigger sample from four lek sites. I have also removed eye spots of peacocks and shown a change (reduction) in subsequent mating success. This paper was published in Behavioural Ecology and Sociobiology but this has not been cited nearly as widely as the Animal Behaviour paper.
HS: Did this paper create a buzz – within academia and outside – when it was published?
MP: My memory is that there wasn’t a huge amount of buzz around this paper, although it did get some attention. Other papers that I have published created a bigger response in the media, such as the paper in Nature 1994 showing evidence for improved growth and survival of the offspring of males with more elaborate trains.
HS: How important has this paper been in your career? Has it had a major influence on the course of your future research?
MP: I think that the peacock work has had a huge impact on my career and it was certainly critical in my obtaining a NERC advanced research fellowship which I held in Zoology at Oxford and which provided the wherewithal to do a further 5 years of pure research.
HS: Have you ever gone back and read this paper after it was published? When you read this paper now, what are the aspects about it that strike you first?
MP: I did have a look at the paper again recently, in response to your questions, and it does seem like something from a different era, where natural history and simple field observations were considered to be important. Times have changed enormously in academia, and it is now extremely difficult to obtain money to do this sort of work. This is a shame, to say the least, as there is so much that we don’t know about the natural world.
HS: If you compare this paper to papers you write today, are there any differences, e.g. in writing style?
MP: I am not sure how my writing style has changed, if it has at all, but how you produce papers has changed.
As you become more senior in academia your job changes from being one where you do everything yourself (from collecting data to analyzing and writing papers) to one where you spend a lot of time applying for grants for other people to work as part of a team. Your job becomes contributing ideas, reading other people’s work and contributing to that, rather than writing your own papers from scratch.
HS: Have you had the opportunity to go back to your study site after the paper was published? Are any of the birds you banded still around?
MP: I wrote a number of papers on peacocks after this one was published in 1991, and this involved doing several years more field work at Whipsnade. However, in 1996, I moved to a new post at Newcastle University, and once I moved to the North-East, it was logistically difficult to continue working at Whipsnade. I continued to work on peacocks at a peacock farm in Norfolk. I have been back to Whipsnade once, a few years ago, and saw very few peafowl. Apparently, there was a big cull when there was an avian flu scare in the UK, as the keepers were worried that avian flu could be passed from the free-ranging peafowl to other animals in their collection. I saw one of my marked birds, and it was begging at one of the restaurants in the park. Flint pit paddock still exists, but it is no longer full of peacocks.
HS: This paper has been cited 360 times (Google scholar) as of today. Do you keep track of these citations, and do you know what this paper gets cited for, mostly?
MP: I do not look at the citations of this paper very closely nowadays, but think it is usually cited as evidence for female choice. Although this is not universal, and in my experience, what people actually cite in a paper sometimes has more to do with what they are trying to say, than what you have actually said!
HS: What would you tell a student who is about to read this paper today? Any caveats? What should he or she takeaway from it?
MP: Probably the most important parts of the paper are the data on individual females. These show two things: one is that females don’t mate with the first male that they approach; they always look at more than one male and this is very good evidence for female choosiness. The second is that they mate with the male that has the highest eye-spot number of those visited. This suggests that the male’s train has something to do with their choice, although it is not necessarily eye-spot number that is being assessed, and it may be something that is related to eye-spot number. It may also explain why males with relatively few eye-spots obtain matings (by being the best of those sampled), and that this doesn’t always result in a high correlation between train characteristics and mating success either within a lek or across several leks.
HS: Among all the papers you have written, is this your favourite?
MP: I wouldn’t say that this paper is my favourite. The first paper I wrote from my PhD work will always have a special place in my heart and that is Female moorhens compete for small fat males which was published in Science in 1983.
In 1971, Paul Dayton published a paper in Ecological Monographs providing experimental evidence for the role of physical and biological disturbances, as well as competition, in influencing an intertidal community off the west coast of USA. Forty-five years after the paper was published, I spoke to Paul Dayton about the making of this paper and the impact it has had on his career and our understanding of intertidal communities.
Citation: Dayton, P. K. (1971). Competition, disturbance, and community organization: the provision and subsequent utilization of space in a rocky intertidal community. Ecological Monographs, 351-389.
Date of interview: Questions emailed on 3 September 2016; responses received on 25 September 2016
Hari Sridhar: How did you become interested in marine ecology?
Paul Dayton: I grew up living a life mostly outdoors, first in Arizona, as my father worked on a ranch and in a deep gold mine, and then moved to Oregon where he worked first in logging camps, eventually trying to make a living selling life insurance after moving back to Arizona. In the logging camp era we started making Christmas trips to a, then very remote, bay near Guaymas, where I learned to snorkel, in 1952, when I was 11 years old. At that time marine life was not well known, as scuba gear was still being developed by Cousteau in Europe. To me it was also scary initially. I had spent most of my life outdoors and was very familiar with terrestrial systems, but this was utterly new and a huge challenge and I was hooked!
Dayton (white shirt, in middle) and friends on a ledge overlooking Shi Shi Beach and Point of the Arches (© Linnea Dayton)
HS: Through reading the Brueggeman interview and looking at your website, I came to know that this paper formed part of your PhD at the University of Washington. What was your motivation to work on intertidal communities for your PhD?
PD: This is independent of the last question. I was already committed to marine ecology and was working with Bob Paine, but my thesis was also much influenced by Gordon Orian’s emphasis on basing ecology on the study of evolutionary processes. I was also influenced by a paper by John Platt about the importance of testing hypotheses, as Paine was doing. But it is hard now for modern ecologists to understand how absolutely dominated ecology was by the dogma that all evolutionary ecology was a result of competition. It was an over-reaction to a long history of density-independent dogma and an ecological focus on using environmental physiology to explain the distribution and abundance of species. But instead of focusing on processes such as predation, facilitation as well as competition, there was an aggressive focus only on competition. This was because the first focus on evolutionary processes was led by charismatic physicists and mathematicians who really did not much care for understanding nature as much as having their models used, and their models were bounded in ways that were not very receptive to predation and facilitation, and many of them went to some effort to downplay the importance of these more realistic processes. I am very dyslexic and was totally unable to understand the beauty of their math, and most models seemed rather irrelevant to the natural world as I perceived it, thinking with pictures as dyslexic people do.
When I first came to graduate school I was diving around Friday Harbor, but the underwater system that I could relate to was already spectacularly studied by Bob Vadas, an excellent student finishing his thesis at the time. So I focused on the intertidal, but focused on some poor questions relating to sea anemones. But in so doing I was also working at sites around Makah Bay where Paine was working. Along with Platt, all of us were much influenced by Joe Connell’s intertidal work, which was very influential in supporting the competition paradigm. But as I crawled around the intertidal habitats of the Washington outer coast and San Juan Islands, I did not see much competition; rather I saw various types of disturbances that ameliorated most potential competition. The potential for space competition was obvious, but many agents that disrupted the competition also seemed common.
Ecology has grown into a discipline of very good, but also very specialized, scientists. Fortunately, I was not influenced by these specialties, and was able to crawl around the very different intertidal systems in the region and try to figure out what processes were at work in each place. And there were all sorts of important factors influencing the patterns. I was most interested in biological questions such as predation, or disturbance such as limpet bulldozing young barnacles and eating small algal recruits, or the facilitation of specific algae that served as nurseries for mussel spat, or refuges from desiccation such as anemones for snails, creating zones of intense snail predation that differed from areas with no anemones. Another form of facilitation was algal overstories sheltering a whole community of small algae. But of course there was some competition, especially in the lower algal dominated levels. But one of the things that is lost by specializing on specific processes, or, importantly, working in a limited number of habitats, is an appreciation of the huge importance of non-biological factors. Every place I worked was physically different, and the differences included the obvious influence of wave exposure and the many critical oceanographic factors determining the recruitment, growth and survivorship of the plants and animals. There were also differences in the rock substrate running from soft sandstone to hard greywacke sandstones to various igneous rock types, and these differences can structure the settlement patterns with all of the subsequent biological interactions. On top of this, in my own areas, the battering by drifting logs was also an important factor. So really, a dyslexic naturalist crawling over this habitat sees all sorts of processes going on at the same time, and the entire spectrum of processes changes from site to site. I did my best to test and describe these processes, missing a lot. The most important lesson for me was that while the habitats are different, the fundamental processes themselves can usually be seen, but they have different ecological strengths from place to place. To really understand the bigger picture, it is good to be able to work in different habitats, to compare the different interactions strengths. But this personal appreciation for seeing the big picture is why I think that those non-naturalists focusing on their statistical dogmas have done so much damage to a general understanding of natural systems. I would say the same thing about those working only with models or in the laboratory. Surly appropriate statistics, models and laboratory research can be extremely valuable, but only when they are tied into real natural history.
Sorry for the long rant responding to a simple question!
Dog dish experiments excluding limpets (lower left), normal density (top) and 2x density (lower right) (© Paul Dayton)
HS: If you don’t mind my asking, how come your PhD supervisor – Robert Paine – wasn’t an author on this paper?
PD: I don’t mind your asking, but really I think you should unask the question and instead ask why is it that most ecologists slap their names on anything they can, including their students research. In those days none of the good ecologists put their names on their students’ papers. I don’t think Paine ever put his name on a student’s paper, nor do I remember Joe Connell doing so, nor Thorson nor Kitching or any good ecologists of the era. I did not do so either. Joint authorships were done when you genuinely worked together on a project, and I put Paine on some of my early Antarctic papers as he contributed a lot. So the real question is why it is so common now, and the obvious answer is that our “fame” seems to depend on number of papers and citations rather than the creative breakthroughs or important advances to a field. I like to think that the colleagues I care about are able to evaluate my “worth” based on, both, publications and independent students not dragging my name around as a “Matthew Effect!” The problem is that our bureaucrats are too lazy to do their jobs well, and want to be dazzled by metrics such as numbers of papers irrespective of whether the papers say anything worth while or those stupid H values that reflect nothing of much importance that I can see. And nobody any more keeps track of successful students we mentor, and here is where I want to stake my legacy.
HS: Do you continue to visit and work in the sites that you sampled during this study?
PD: I so wish I had done so. I always wanted to but only got back a couple times. I offer the normal excuses: I was busy with other time-consuming projects, mentoring wonderful students who really mentored me, and I was totally committed to spending my summers camping with my kids until they got into high school.
HS: Would you remember how long the writing of this paper took and where you did most of the writing? Apart from your supervisor, Robert Paine, were there other people who you were regularly discussing your work with at the time?
PD: Good question. I got a tremendous amount of mentoring by Bob Paine, Joe Connell, and Bob Fernald, but most of my real learning came at the hands of graduate students. Graduate students shared large offices and most of us did our writing at home. I wrote it all by hand, as I write badly and it needed lots of smoothing. My cohort of graduate students, especially Rick Vance, Bruce Menge, Chuck Birkeland and Sally Woodin broke their butts trying to teach me math and theory – that they failed is no fault of their own as I now understand the severity of my dyslexia. In the end, my good wife did all of the statistics in the paper, and helped with my prose. I finally sat in the kitchen and painfully typed all of the piles of scribbles, and my committee did an excellent job reading it and helping me make it literate! But it did not really take very long, as I had thought about it a lot and knew pretty much what I wanted to say. I think I started writing in February and was mostly finished in early summer.
HS: How were the figures in the paper drawn?
PD: By hand! In those days we had sets of frames that we used to draw lines, curves and letters, but they were all carefully traced by hand.
HS: Could you give us a sense of what your daily routine was during the fieldwork for this study? Did you mostly work alone or did you have people to help you?
PD: Entirely alone. I worked in two areas that were several hours from Seattle, where I had to return to teach labs for my salary until the end. It is documented in my thesis, but I think I was in the field over 60% of the 5 years I was in graduate school. The outer coast sites were rainy and difficult to get to, but very rewarding and fascinating for their high diversity and all of the fascinating interactions. The tides were often in the middle of the night, and I spent the day fishing for Salmon from Bob Paine’s tiny boat. I slept and ate in my small 4-wheel drive vehicle. The San Juan Island sites were much dryer and more difficult to work because the rock was so hard. I struggled to maintain the cages. But there I had the luxury of a house to stay in and I was better able to work up data and get caught up. I spent my free time solo diving, looking at sea star foraging biology. At the time, I think I was stressed trying to keep up with all the driving and fieldwork and keeping up with the data, but in hindsight those were absolutely the best times of my life. Bob Paine was a wonderful warm friend as well as a mentor and he kept reminding me how lucky I was, and he sure was right.
Eagle Point Study site, San Juan Island, Washington, and the old International Scout Paul Dayton, mostly, lived in. Dayton says that this area is, today, totally blocked by huge mansions and not accessible for scientific study (© Paul Dayton)
HS: Did this paper have a relatively smooth ride through peer-review? Was Ecological Monographs the firs place this was submitted to?
PD: Yes and Yes! I marked up the actual thesis very carefully, in the first month of my job, the generous Department secretary retyped it, and I submitted it within a few months of defending the thesis. The reviewers were Peter Franks and Joe Connell and both were very careful and constructive and helped me in many ways, but it went right through. I don’t know who reviewed the 1972 Postelsia, 1973 right-for-the-wrong-reason and 1975 algal papers, but they were all very constructive and I did not have the nightmare that many young students experience now. The people in Paine’s generation were very constructive and helpful, but unfortunately those of my generation seem hyper-critical and often hostile. I very much regret this situation.
HS: Could you give us a sense of what kind of impact this paper had on your career and on the future course of your research?
PD: The Ecological Society of America recognized it with their Mercer Award, which meant a lot to me. In the beginning, it did not have much effect on my career and I am not sure it influenced my tenure promotion. By that time, I had published several pretty good papers from the inter-tidal, the Antarctic and the kelp system. I would expect that the Mercer Award helped with the promotion, but I don’t think many people have actually read the 1971 paper, even though it is heavily cited.
HS: Today, 45 years after it was published, would you say that the main conclusions of this paper are still true, more-or-less?
HS: Yes. Even without the reasonable caveat of putting it back to the state of the science then, I immodestly think that the conclusions are pretty much true today.
HS: If you were to redo this study today would you do anything differently?
PD: I would write it very differently. It is heavily cited but not read. People cite and recycle something apparently without realizing what I had done. Sometimes this is reader laziness, but in this case there is no doubt that the paper is very hard to read. That is entirely my fault. I still struggle with my prose, but I dearly wish I had struggled a lot harder with that paper, perhaps breaking it into several papers.
The other thing I would emphatically do differently is bring in all the different strengths of the processes as one goes across this huge environmental gradient from Tatoosh Island to Colin’s Cove. I was so entrained into the battle with the competition folks that I focused too narrowly on my message, that in the real world nature is much more influenced by disturbance than resource competition. I drove thousands of miles working the two areas at the same time and really completely failed to discuss the obvious lessons about the physical effects of the shifting environmental conditions across that gradient.
HS: You say “The most important physical factors correlated with differences in the relative distributions and abundances of the important sessile species in the intertidal are (1) wave exposure, (2) battering by drift logs, and (3) physiological stresses such as desiccation and heat”. Today, do these three factors continue to be the most important?
PD: If I said that it represents another terrible omission. Most of the focus of the paper and my career is on the various evolutionary roles of biological interactions: competition for potentially limited resources, predation, disturbance, and facilitative interactions. Certainly those three factors are critically important, but I would also add biological interactions!
HS: This paper is today a ‘citation classic’. At the time when you were doing your work did you anticipate at all that it would have such a big impact on the field? Would you know what the paper mostly gets cited for, i.e. is it cited appropriately most of the time?
PD: I was young and insecure and I hoped all marine ecologists would read it and agree with the idea that disturbance trumps competition in most systems. It took awhile, but eventually I think that the message did get across. I think that most of the citations I have seen are appropriate and I am very grateful that my peers recognize it. I think my colleagues are very generous with their citations and I am grateful.
HS: Have you ever read this paper after it was published? When you compare this paper to ones you write today do you see any striking differences?
PD: Not really: it is hard for me to read also! Once in a while, I go back and dig something out to remind myself what I did. Surely, it would never even be reviewed now because of its length. This is probably a good thing because it would be more readable, yet I have always enjoyed my “story telling” approach to ecology, that involves an understanding of the big picture in time and space. Even as a student I realized how important scaling time and space were, and that would be lost if the paper were to be chopped up as demanded by today’s standards.
HS: Would you count this as one of your favorites, among all the papers you have published?
PD: I am very proud of the paper and grateful for the recognition. And I am still proud of the total thesis, although I don’t think it was as good as the one Bob Vadas did before me. Students then were doing interesting projects and I think that there were many good theses. Frankly, I am more proud of a couple of my kelp papers, and the one I am most proud of was done in the Antarctic at the same time I was doing my thesis. This was published in 1974, and the reason I am proud of it is that it was done in two brief and difficult field seasons, but we had to reject the entire research paradigm that we based the project on to start with. We had to switch questions in the field and focused on asteroids and sponges, and in the second season none of our experiments had worked because we totally underestimated the slow growth rates. At that point, I had to find a way to estimate the predation rates and consumptions over a year. This was done using the ecosystem approaches of the era that I did not know and had to learn in the field in Antarctica. Bob Paine visited us there, and was very helpful as we struggled to estimate the effects of the predators on the sponge populations. These days, ecosystem and population people rarely interact, and have developed very different specialties, but being able to synthesize both approaches made that paper possible.
HS: What would you say to a student who is about to read this paper today? What should he or she take away from this paper written 45 years ago?
PD: I would tell her that this paper is very difficult to read, but it has a lot of interesting information that might be useful to her. I would explain the value of story telling as a means of understanding nature, and that there are several interesting stories in the paper. I would suggest that as she reads it she copies the table of contents and lists the various vignettes or stories in the paper, and at the end see if she can synthesize those that are of interest to her into a big pictures story that makes sense.
HS: Thanks so much!
PD: My pleasure, sincerely. Thanks for including me in your project. I just did this at home and realize it is more complete than I would have done in an interview because I had to write it in short bits of times getting the grandkids ready for their sabbatical! But I kept thinking that if there is anybody interested enough in the paper or in me, that there are a lot of fun stories in the oral history I did with Peter Brueggeman. The dynamite story comes to mind as something that is simply not conceivable today and people find it amusing. If it is possible I suggest that you send them to Peter’s web site to read it if they are interested (and also here for other Scripps oral histories) .
Paul Dayton in Portage Head, study site, Olympic Peninsula, Washington (© Linnea Dayton).
In a 1990 paper in Nature, David Reznick, Heather Bryga and John Endler, showed, through an 11-year experiment on a natural population of guppies in Trinidad, that predators can cause significant life-history evolution. Twenty-six years after the paper was published, I spoke to David Reznick about its making, the influence it had on its career and what we have learnt since about life-history evolution in guppies.
(Interview conducted via Skype on 28th July 2016)
Citation: Reznick, D. A., Bryga, H., & Endler, J. A. (1990). Experimentally induced life-history evolution in a natural population. Nature 346: 357-359.
Hari Sridhar: Before this study, you had already done a lot of work on life-history and evolution in this system. What was your motivation to do the work presented in this paper in relation to all that you had done before? At what stage in your career did this come?
David Reznick: My original motive for going into research was to test some aspect of the theory of evolution in nature. And to do experiments. Evolution had largely been dealt with as a historical discipline, or in work on model systems in the laboratory, like fruit flies. I felt that it should be possible to look at evolution in real time. I was originally inspired by work by Janis Antonovics on heavy metal tolerance in plants, which was coming out in the 1960s and 70s. Janis was seeing evidence for evolution on timescales of centuries, but I felt that something more might be possible, based upon what I’d learnt in population genetics. My earlier papers that led up to this were really to develop the potential to do this experiment. The first question was to consider the natural history of guppies in Trinidad. I had been to a seminar by John Endler where he had talked about localities where guppies lived either with or without predators, and how the predators had shaped the evolution of male colour patterns. What I took from that talk was that those localities differed in the risk of adults experiencing mortality. When there are predators, adult male guppies showing colour were at risk of being eaten, but when predators were absent, males that were mature and showed colour were at much less risk of being eaten. That’s the only way Endler could have gotten his result. For me that paired well with life history theory. There’s a body of theory developed in the 70s that predicted how life history should evolve in response to a change in the risk of adult mortality. This work on guppies gave me a link to a specific facet of evolutionary theory that made a prediction. It meant that I could make that prediction and test it. The first step was to actually see whether or not there is a pattern in nature that was consistent with the prediction – whether or not guppies that lived with predators were on average younger at maturity and more rapidly developing and devoting more resources to reproduction than ones that lived without predators. That’s what the earlier papers had accomplished.
HS: You said you were inspired to do this work after hearing a seminar by John Endler. Do you remember when and where this was?
DR: I do. The talk was given at the Academy of Natural Sciences in Philadelphia in October 1977.
HS: At this time, had you already finished your PhD?
DR: I was doing my PhD at the time and I was working on a very similar problem. I was working on mosquito fish from Illinois and North Carolina and New Jersey and looking at life histories and variation among populations in life histories. And it was approaching the point where I might have been able to do something like I did in guppies. I had found farm ponds in Illinois with introduced mosquito fish, of which some had and some did not have sunfish (family Centrarchidae) in them. So the question was whether or not there is evidence of life history evolution there. So when I went to John’s seminar, my mind was primed, and his system was much more attractive for a variety of reasons. I was beginning my fourth year of graduate school, but after I saw his seminar I wrote the sort of proposal that we were encouraged to write for our qualifiers as second year students. And I gave it to my committee in December that year and asked them to consider letting me change my PhD project. They liked the paper. They thought it was very good and worthwhile for me to, not really discontinue the work on mosquito fish, but to put it on a back burner, and switch to guppies. So the guppy work papers published in 1982 and 1983 were from my PhD thesis, which I submitted in 1980.
HS: And did you continue working on guppies for your postdoc?
DR: Well no. At the point when I finished my degree I had no papers and got nowhere on the job market. But I had this idea to transplant guppies and predators and study evolution in real time. So I wrote a proposal to the National Science Foundation (NSF), but I wasn’t allowed to be a principal investigator on the proposal. So I found somebody whose name I could put down as Principal Investigator and submitted it before I finished my degree. Then by the time I finished my degree, the proposal was funded and it included my salary. I was then, what I described as, an incipiently unemployed research scientist, meaning that I was paying my own salary with my grants.
HS: This paper has three authors – you, John Endler and Heather Bryga. How did this group come together?
DR: The connection with John Endler was his seminar in 1977. I went out to dinner with him that night and said: I have this idea based upon your work. He was very supportive. I first went to Trinidad in 1978 – in March and April of 1978 – and he was there then and guided me. He gave me all the kind of background I needed to be able to work there – he took me out to the field, showed me how to identify the fish, showed me where I could go to collect what I wanted, etc. And I continued to interact with him after that point. In fact, the experiment in the 1990 paper is one that he initiated in 1976, which he talked about in the seminar I saw, and based on which a publication came out in 1980. So there is a natural and continuing connection between us.
Heather Bryga was my lab technician. She was an undergraduate who started working with me when I began as a faculty member in UC Riverside in 1984, Later I was able to hire her and pay her as a full-time technician with my continuing support from the NSF. Heather was the one who oversaw the lab work. I was still in the lab a lot those days but not always. She is the one who sort of kept things on track.
HS: In the paper you say you reared the descendants of these fishes through two generations. Where was this done? Did you bring the fish back to the US?
DR: Yes. It’s interesting, I was looking at the paper the other day and thinking – Nature papers had, I think, a 1200 word limit, because of which you can’t see what you need to see in that paper. So the key sentence, where it says that, refers you to earlier papers. You would have to go to the earlier papers to read the methods. What I did was I collected wild adult females from the two sites, brought them back to the laboratory at the University of California, where I had a lab in the Biology Department vivarium. The experimental side of the lab was really like a fish file system since I had hundreds of two-gallon aquaria and reared one or a few fish per aquarium. I isolated each female in her own aquarium. Guppies store sperm, so each female produces a series of litters of babies, and they became a numbered pedigree. I reared them to maturity and separated males and females before they matured so I had virgin stock. Then I did crosses among the different pedigrees. The cross design was such that each wild caught female was equally represented, and all crosses were unique. There was no sib-sib mating. So it meant that my first lab generation was mated to produce the second lab generation that evenly represented the genetic diversity of the original sample from the field. The goal in doing that was to separate out environmental effects and maternal effects from what I wanted to evaluate, which was genetic differences among populations. By working on grandchildren, the idea was that the environmental effects and the maternal effects had been separated out. They were no longer confounding feature of the design.
HS: In your email to me, you mentioned that you are going back to Trinidad soon. I’m assuming that means you are still working there. Do you continue to work in the same sites that you sampled in this study?
DR: No, our main work now is located in a neighbouring drainage. We have gone well into the headwaters of what’s called the Guanapo River. We still do, sometimes, work in those old sites. Those sites are a living resource and all the introduced and evolved populations are available for sampling. For example, we have a proposal that will be submitted this week, to study the genetics of adaptation in guppies. Part of that will be to compare guppies within a river that live either with or without predators, but another part will be to take advantage of the experiments, where we know which the ancestral and descendent populations were. So these sites continue to be a valuable resource for looking at the evolution of various traits. I and other people continue to use them. But I’m not doing specific work at those sites. I just occasionally use the fish for studies.
David Reznick hiking upstream to one of his study sites where he and colleagues are currently performing experimental studies of evolution in guppies and killifish (© Lynn Johnson)
HS: Have those sites changed a lot since the time you worked there for this study?
DR: The Aripo tributary is pretty much intact. It’s in good shape, and the main site downstream where we collected the guppies that lived with predators is okay. But other parts of it..you know, right now what I’ve heard is that in the last year, a land squatter – I mean somebody who didn’t own the land but has cleared a section of forest nearby –might have modified the lower channel of the tributary that was the basis of that 1990 paper. This has happened before; I’ve seen people come and try to garden there. It’s hard because it’s not very good soil and its very steep. In the past they have used it for a year or two and given up and left. Further back in the forest the site is still in very good shape; there is no serious modification there. But a lot of the sites I used to work on in Trinidad have changed considerably. In the other introduction that I started in 1981 on the El Cedro River, the downstream control – the ancestral site – is very severely modified by human activity.
HS: Are these sites protected?
DR: Well [laughs] technically they are National Forest and should be protected, but they are not.
HS: Could you tell us a little about how the writing of this paper happened. Did the three authors ever get together in one place, or did all the discussion happen over the phone?
DR: I wrote the first complete draft on my own. At that point, John Endler was in Santa Barbara, which is, about, a 2.5-3 hour drive from here [Riverside]. So I just drove to Santa Barbara and we sat down at John’s computer and reworked the paper together. And then I submitted it. I can’t remember if Heather Bryga read or commented or participated in the writing at all.
HS: Do you remember how long it took you to write the first draft?
DR: That’s interesting. I, actually, got the results in 1988. But the inconvenient event at the time was that I was getting a divorce, so I wasn’t able to work on it as quickly as I would have otherwise. I think, I wrote the first draft fairly quickly. I can write reasonably quickly and I don’t think I spent more than, maybe, four sessions of a couple of hours each to write that paper. Then, when I met with John, I think we spent 2-3 hours working on it together on his computer.
HS: That is really quick! At that time, did you have a specific writing routine, i.e. with regard to when and where you wrote?
DR: Yes, I write in the morning. I do things like outlining and working on figures and tables and things like that in the night. In terms of writer’s block, I always tell myself that outlining isn’t writing. Outlining is just putting your ideas down and I can do that any time of the day. So I tend to work on outlines of papers and sketch out the order of ideas in the evenings, and then I get up and do the writing, the actually sentence construction, in the morning.
HS: Where do you write, usually?
DR: At that time, I was living in Riverside, in a small town house that I had just gotten, and did all the writing there, at the dining table.
HS: Did this paper have a relatively-smooth ride through peer-review?
DR: Yeah, it did. I got word of it when I was in Trinidad. They just asked for some small changes. It was not controversial, in that regard.
HS: How did you make the figures for this paper? Did you hand-draw them?
DR: 1990.. No, I think I just used some kind of computer program we used for drawing figures then. I think Heather Bryga did those figures, or certainly helped with them.
HS: How was the paper received when it came out? Did it get a lot of attention?
DR: Oh my, it changed my life. It appeared on the front page of the New York Times and the World Herald Tribune and in many other newspapers. I was called to do a TV interview, but I couldn’t make it. They woke me up at 8 am and asked if I can be in downtown LA at 9 am! I, also, got many invitations for seminars. It did a lot to help establish my career.
HS: Why do you think this study attracted so much attention?
DR: Because it showed evolution in real-time. You take it for granted now. It’s like no big deal now to say – ‘Oh, I study contemporary evolution’, since so many others have done it. But what people don’t realise is that this change in how people would respond to the study today versus in 1990 is what you could think of as a paradigm shift. When I proposed the experiment in 1980, in the original grant I wrote for the NSF to do this experiment, people used to smile at me and say – “it’s a good idea and we hope you live long enough to see something happen.” Even Jerry Coyne, who is a very prominent evolutionary biologist, saw me present this in a seminar in 1984 and said – “I hope this works. It’s a good idea.” It seemed like I was expecting a lot, to be able to see any kind of change over such a short time-scale. The Grants‘ work was coming out just then. Their work was 1980-81 and it was getting a lot of attention. Initially, however, they were looking at selection, not evolution. They didn’t nail it down as evolution until a couple of years later. But it wasn’t experimental work, and it wasn’t linked to a body of theory that made specific predictions. So I think the thing that was attractive about my work was that I had a prediction based on a body of evolutionary theory and I went and found a plausible situation in nature where we could test it. By the way, this is the second paper. A paper by me and Heather Bryga appeared in 1987, on the earlier experiments showing the evolution of male life history traits, and it got no attention at all. This was from the the El Cedro river experiment, but in that we looked for evolution after only four years. That seems kind of bold now, but I was an assistant professor looking for tenure, so I figured I would take a chance and see if it worked. And it did work, in the sense that the male traits had evolved, but there was no evolution of female traits. The 1990 paper was based on an eleven year experiment, and there the female traits showed up. But if you look at Table 1 in this paper, you will see the 1987 experiment is also in the left hand column. That’s from the earlier paper.
HS: What kind of impact did this paper have on your career?
DR: I think it made me known in my university. And it got me a lot of seminar invitations. I had linked it to my earlier papers, so it attracted more attention to the whole sequence of the work. But I will tell you what the biggest impact was, which I find hard to talk about. My choosing to become a scientist didn’t go over well in my family. For them, it was okay if that’s what I wanted to do, but my father wanted me to go into the family business or to veterinary school, which I had gotten admission into. Becoming a scientist seemed like an eccentric and not so meaningful thing to do. But you know, even though they didn’t understand my work, seeing me in the newspapers gave it legitimacy in their eyes. You don’t usually hear about this, but that really was, more than anything, the most important consequence of that paper.
HS: How did this paper influence the future course of your research?
DR: The other thing I was trying to work on at the time, which I was having some success with, but which I didn’t publish till much later, was the demography of natural populations through mark-recapture. Up until this point in time, the assumption was that if you live with a predator your probability of dying is higher. That seemed reasonable, but I wanted to actually prove it. So between 1986 and 1990 I got NSF money for detailed mark-recapture work. I was marking guppies using acrylic latex paint that I made less viscous by diluting it with Teleost Ringer’s solution. I found that, in a lot of these streams, the probability of catching a fish if it was alive was exceedingly high. Said differently, the odds of not catching the fish were so low that I could interpret the number re-caught as being very close to the number still alive. So it became a way of estimating mortality rate and I could show that, in fact, mortality rates were higher in streams with predators.
There was a major revolution in how people perform and analyse mark-recapture data that came between when | began and finished the work. The new statistics let you discriminate between causes for not seeing an individual in a given census. It may be because it died, emigrated or was present but not caught. If you sample properly you can get independent estimates of all of these things. I had collected data in a way that would allow me to know if emigration or escaping capture were important issues because they could bias the data, but I had not collected data in a form amenable to the new sorts of statistics. This means there was a special burden to address these potential sources of bias. I delayed publishing so I could add some extra experiments to convince people the data were okay.
One inspiration for the delay and extra work is that I presented my results at a conference in France with one of the founders of the new theory in the audience (J.D. Lebreton). He raised his hand and announced that he did not believe I could catch all of the fish. The extra work I did showed that I can, indeed, come so close to catching them all, and that the data were okay.
The weird thing though was – and this paper didn’t come out until 1996 – that the shape of the mortality curves for the high- and low-predation guppies was not what it needed to be, to be consistent with the original theory that predicted how life history should evolve. The original theory was based upon differences among age-classes in risk of mortality. And what I found was that in high-predation localities, all the age-classes had a higher risk of mortality to an approximately equal degree. And the theory I was using said they shouldn’t evolve, and that you couldn’t get evolution unless there was heterogeneity among age-classes in risk. At first, the result was upsetting, but then I realised – ‘Well no, I had seen them evolve!’ I had already done it. And so it wasn’t a question of whether or not they evolve, or whether or not predation had anything to do with it, but it still said that there is something more going on. And that has led directly, in two ways, to the kind of work that I’m doing now. First, the reason the low-predation life history evolves is not because of the lower risk of mortality, but because of the indirect effect of population densities being much higher and depleting the environment of resources. It’s a version of what people now call eco-evo. interactions. In 2006, I got the biggest grant I’ve ever got – a multi-investigator grant – to use guppies to evaluate the importance of eco-evo. interactions in a natural ecosystem. That was a partnership that included theoreticians, geneticists and ecosystem ecologists. That work still goes on. The second thing was that, once we perfected the mark-recapture, it became possible to repeat the kind of introduction experiment we had done earlier, but to begin with marked individuals. We could then census them monthly, mark all new recruits, save scales from each of them, and get DNA from the scales. Using the DNA, we can construct pedigrees, quantify individual reproductive success and look at evolution in a very different way, i.e. as variation in individual reproductive success. Then we could associate this variation in reproduction with individual-based traits we had measured. One of the nice things about this system is that, at each stage, as I learnt more, I was able to use the learning to answer a greater diversity of questions. I continue to work on guppies in Trinidad till today and am, in fact, just finishing a manuscript on them.
HS: It is now 26 years since this paper was published. Would you say that the main conclusions still hold true, more-or-less?
DR: Yes, and the result has proved repeatable. In the new experiments we have four replicates, and we show that it’s happening, but we also have a much better idea about why it’s happening, than we did then. The aspect of that paper that didn’t hold up was that it was written around the idea that it was differences in age-specific mortality that caused the life-history patterns that we saw. As I said earlier, we now know that that’s not the explanation. Indirect effects of predators and density regulation are playing a very important role.
HS: If you were to redo these experiments today, would you change anything, given the advances in technology, theory, statistical techniques etc.?
DR: Well yes. In the new wave of experiments we did, we did change things. In the earlier experiment, I just collected a bunch of fish and introduced them. Actually John Endler set that experiment up, the one in 1990. I had done the one in 1987. But in both we just collected a mixture of fish and put them in. What that meant was that we didn’t have complete knowledge of who went in or what their genetic makeups were. In the new experiments, what I did was to collect juveniles from the source site, rear them to maturity in single-sex groups, mark them, mate them, collect scales from all of them, photograph them and then introduce them. Then we continued with the same mark-recapture for every new recruit. Through this we know we know about individual movements and the community in which they are growing. And we have their DNA, using which we can work out their pedigree. So the recent experiments are yielding a much richer body of information. None of this was conceivable when this work was done in the late 70s or early 80s.
HS: Do you continue to collaborate with John Endler on this work?
DR: Yeah, actually we do. For a long time we didn’t, but he was the co-Principal Investigator on the grant I got from 2012 through 2016. He is looking at the evolution of colour patterns again, but using all of his new methods that weren’t available in 1980. I could tell you a little bit about that if you want to know.
DR: So after that work in the 80s-early 90s, John almost became like a neurophysiologist. He was interested in, sort of, the neurobiology of how organisms perceive colour, and in the innate structure of colour in the environment and how light changes through the course of the day. He developed these predictive models that integrated the perceptual sensitivity of females with the colour spectra of reflectance of the males, to ask whether or not the pattern of evolution would affect the way females perceived males, or how predators saw males. He was able to show that, in some circumstances, you could become more brightly coloured and attractive to a female but yet not more conspicuous to the predator, because of differences in their visual sensitivities. In the current experiments, we have two localities where we have thinned the canopy to increase primary productivity which also changes light falling on the stream. The question is whether or not the change in light would affect the colour patterns of males and how they were perceived by females. John used that as an experimental treatment to look at male colour pattern evolution, and we are now at the point where we can write the papers. We know that the canopy has a significant influence on the evolution of structural components of male colour, the structural green and blue. Part of the guppy coloration is structural and part of it is pigments, and we now have clear evidence for the evolution of the structural colouration. John will now be plugging in his models to see whether or not this is predictable based upon the nature of the light and nature of the visual sensitivity of the females. Darrell Kemp is also playing a big role in this work.
HS: In one place in the paper you compare the results of the four- year study and this 11-year study, based on which you argue for the need for long-term field experiments. In the years since this paper was published, to what extent do you think that has happened?
DR: There’s been some. I’m actually giving a Skype talk in October to Florida International University where they have a Long-Term Research in Environmental Biology (LTREB) grant. That’s an NSF programme that I think came into existence in the 70s. There is a lot of talk about the importance of long-term work. Experiments like we are doing, there are some out there, but there aren’t many. The thing that has happened instead is long-term mark recapture on model systems. That’s mostly a British type thing – Soay sheep, red deer of Rhum, the meerkats in Africa, and various great tit populations. Long-term mark recapture on individual populations of birds has really blossomed. There’s a lot of that kind of work.
HS: Towards the end of the paper you say your results demonstrate “the importance of predation in moulding life history evolution in guppies, though of course other factors may be important.” Subsequent to this paper, were other such factors discovered?
DR: Yeah, the indirect effects that I told you about is one factor. Another is resource availability. When you talk about density dependence what it means is that guppies are adapting to themselves. People don’t usually think about density-dependence that way. The eco-evo. interaction idea was alive dating to about 1961 but it wasn’t mainstream at all. It was silent in the background, but now this idea is very much in the fore front. That’s the other main factor that emerged with guppies. I wasn’t thinking of that precisely then but I was wondering about the importance of resource availability, because it seemed to be a feature of the head-water streams versus the downstream localities. The head-water streams are much darker because they have completely closed canopies, which affects light and productivity.
HS: In the final sentence of your paper you say “The widespread evidence for size-specific predation in other species suggests that this could be a common factor in life-history evolution”. Has work after this paper found support for this suggestion?
DR: That’s a good question. I’m trying to think. In the bird literature, that wasn’t a new idea, conflict between predation and the ability of parents to provision their young. Certainly within the field of bird life history evolution, which is the biggest area where that kind of work is being done, predation emerged as a big deal. Tom Martin was reading the guppy papers at the same time as he was independently developing the idea that predation was the primary factor driving evolution of life histories of birds. It wasn’t original to him but he did more than anyone to develop the idea and show that it was important in bird evolution. I’m trying to think of other organisms. I know that it has turned up. Now, life history evolution has kind of faded in to the background. It’s not a premier topic as it was then, but I think it is fair to say that predation already was and it’s grown since, as an important factor in shaping how life histories evolved.
HS: This paper has been cited over 800 times. Do you have a sense of what it mostly gets cited for?
DR: I think for the idea of contemporary evolution and experimental studies of evolution in nature. Like I said you may have always grown up with the idea that evolution is contemporary and you can see it happening in real time. But that was a new idea then, and I think this paper has maintained some interest for helping pioneer that.
HS: In the 26 years since it was published have you ever read the paper again?
DR: I actually read it again yesterday because I was meeting with my undergraduates. I don’t always assign my own papers, but I figured it was a reasonable one to introduce them to the system. Maybe it was because you had made me think of it with your email. But at other times too, I remember looking back at it, every once in a while. I’m always impressed with how brief and simple it was. I don’t know if you noticed, but it doesn’t report any sample sizes, which is very embarrassing.
HS: What strikes you most about it when you read it now?
DR: The thing that strikes me was that it was simple. I guess I try to write papers like that today as well, you know, have a short simple sentence structure and not clutter it with extraneous ideas. I guess I didn’t realise I had figured that out at a pretty early stage in my career. I remember, one of the books I read about writing was “The Elements of Style” by Strunk and White. I had read it in 1988-89, sitting at my dining table. So that was fresh in my mind at the time I wrote this paper. So when I read it now, I’m glad to see did an okay job with it, in terms of simple sentences and being clear.
HS: Would you consider this one of your favourites, among all the papers you have published?
DR: Oh yes, it still is. It still serves as a standard I try to live up to, with the work that I do now.
HS: What would you say to a student who is about to read this paper today? What should he or she take away from it?
DR: They should take away the idea that evolution is a contemporary process happening in real time, and it’s one that can be studied empirically with experiments in nature. It’s a question of finding the appropriate setting to do it. So the contemporary nature of evolution is probably the most important message. Also, that it’s possible to extract, from evolutionary theory, specific predictions that can be tested in a natural setting. Finally, in terms of how the system has developed over time, it’s also a statement for why it’s good to do things in nature and not just do them in the lab. The lab version of reality is highly abstracted and it cannot capture the range of interacting factors that you see in nature. People will say you do it in the lab because you can control it and be clear about what’s going on. That’s true, but if you want to know why animals or plants are the way they are in the real world, then you need to work in the real world, because the full scope of factors that interact in shaping evolution can’t be anticipated or replicated in the lab. I made a similar argument one time, way back when people asked me why I wasn’t doing these experiments in the lab. I said it’s because I want to know why things are the way they are in the real world, and I don’t have faith in the lab being able to reproduce that. The way this project has developed has shown that there’s no way that any lab work could have led me to an understanding of ongoing interactions between ecology and evolution. You just can’t capture that in the lab. I couldn’t have anticipated that when designing the lab study. Therefore, I think it’s important to work in nature whenever you can.
In a paper in The Annual Review of Ecology, Evolution and Systematics in 2000, Peter Chesson attempted to “tame” the wide array of models and ideas about species diversity maintenance, especially in the context of species coexistence in local communities. Chesson’s paper went on to become a cornerstone of modern coexistence theory. Sixteen years after the paper was published, I spoke to Peter Chesson about his motivation to write this paper, and how research on species coexistence has progressed since then.
(Questions emailed on 3rd September 2016; responses received on 18th September 2016)
Citation: Chesson, P. (2000). Mechanisms of maintenance of species diversity. Annual review of Ecology and Systematics: 343-366.
Hari Sridhar: Could you share with us your motivation for writing this paper? Was it written following an invitation from the journal?
Peter Chesson: I wanted to write this paper for several reasons. The first was that there was a general lack of appreciation of several important ideas in competition theory with regard to what it means for species to have similar niches. There seemed to be little appreciation that average adaptedness to the environment, what I called in this paper “average fitness,” needed to be considered very differently from the details of how a species uses the environment. It always seemed obvious to me, but it took me years to realize that it was not obvious to everyone. In addition, I felt there was not enough general appreciation of the theoretical advances that had been made to incorporate the role of environmental fluctuations in coexistence theory. Finally, I felt that although there are lots of common themes in coexistence theory, many people seemed to think of each hypothesis rather differently, when many of them could be united. These were my motivations. I was not invited by the journal to write the paper. I submitted a proposal three times in successive years before it was accepted.
HS: Stepping back a little, could you tell us how you got interested in the topic of species coexistence? Which came first: an interest in ecology or an interest in mathematical modelling?
PC: I have been fascinated by ecology since I was a small child. I developed an interest in mathematics as a teenager, and ultimately decided to do a mathematics degree with the idea of applying it in ecology. I got interested in species coexistence after seeing Bob May‘s treatment of it in his book, “Stability and Complexity in Model Ecosystems“. My imagination was captured by Robert MacArthur‘s utilization function idea, but also, I thought there could be a better development of the role of environmental fluctuations than appears in May’s book.
HS: How long did the writing of this paper take? When and where did you do most of the writing?
PC: It took me about two weeks of concentrated effort to write the paper as I rushed to meet the deadline for submission. Naturally, I had been thinking about the issues for a long time. Most of the writing was done in my office at UC Davis between teaching terms when I could focus on it.
HS: You acknowledge P. Abrams for his help on this paper. Can you tell us a little more about how he helped?
PC: After the paper was submitted, I sent it out to more than a dozen colleagues. The majority of people who responded were enthusiastic, but had no concrete suggestions. Peter Abrams gave a series of critical comments that helped me bring out more clearly some of the points that I was making. I was glad to get these comments from him because of his often critical appraisals of the field as a whole.
HS: At the time when you were writing this paper, did you anticipate at all that it would have such a big impact on the field?
PC: I certainly hoped it would have an impact, but I did not expect that the stabilizing-equalizing dichotomy that is highlighted in the abstract would have such a life of its own.
HS: Would you know what this paper mostly gets cited for? Would you say that most of the citations are appropriate, i.e. that people understand the theory correctly?
PC: The paper gets cited in two ways. Most commonly it is “coexistence theory” as a general reference or for a specific hypothesis that authors presume I have discussed in the paper, regardless of whether I actually have. Naturally, that leads to a large number of mis-citations. Some citations are for the exact opposite of what it does say. These are primarily for cases where it takes on the conventional wisdom with the regard to environmental fluctuations or natural enemies, and the citing authors have either not understood what I have said or have not bothered to read the paper. Other citations are for the stabilizing-equalizing dichotomy, which by the way does not refer to strict alternatives. A coexistence mechanism can be both stabilizing and equalizing, and this fact is clearly demonstrated with examples in the paper, but this subtlety is often lost. I think many people get the basic ideas in the paper, but we have a serious problem in ecology that education about theory and the use of models is not widespread or in depth. Thus, for most people, a deep understanding of the ideas in the paper is not possible. However, the paper itself seems to have inspired some labs and some intrepid graduate students to dig more deeply into theory, and has led to many applications of at least some of the ideas.
HS: Did this paper have any kind of a direct impact on your career? How did it influence the future course of your research?
PC: It has not changed any major plans in my research, but it does seem to have drawn more attention to my work.
HS: Could you reflect on the kind of impact this paper has had on empirical research?
PC: The most obvious impact I can see is various efforts to investigate the stabilizing-equalizing distinction. There have also been numerous effects to apply that idea in related areas of ecology and evolutionary biology. The major impacts may be more subtle in providing the understanding required for better interpretation of empirical studies.
HS: If you were to rewrite this paper today, would you update the theory in anyway?
PC: There is much to update really. The most obvious update would be the much more comprehensive understanding that we have today on the role of predation in species coexistence. The paper had just a small section on this. In effect, it has been updated though in my essay on “Species Competition and Predation” in Robert Meyers’ Encyclopedia of Sustainability Science and Technology. Another big update would be more on the effects of spatial and temporal scale, especially spatial scale. Early in the paper, I make the statement, “Many models of species coexistence are thought of as models of coexistence in some defined local area. However, to make any sense, the area addressed must be large enough that population dynamics within the area are not too greatly affected by migration across its boundary (103). At some spatial scale, this condition will be achieved, but it may be much larger than is considered in most models and field studies.” This is actually a warning against the focus on the “local community” in empirical studies. At the time, I did not have much to say about how to get around that problem. But that has changed with the further development of Scale transition theory, which provides an adequate framework now for how to deal with multiple spatial and temporal scales including non-stationarity of the environment in space and time, which we need for addressing long-term climate change. Finally, an update would provide a better guide on how to use the various concepts empirically.
HS: In the last sentence of your paper you say “Allee effects in sparse (low density) populations and stochastic extinction in small populations both potentially limit how similar the niches of coexisting species can be when similar niches mean sparser or smaller populations. These possibilities deserve further study as they have the unique property that they would still work when species are equal in average fitness”. Subsequent to this paper, have these aspects been researched further?
PC: In fact, I am not aware of serious research by theoretical ecologists following up the point on Allee effects. However, the mathematical literature on dynamical systems in ecology has been investigating Allee effects mostly for the interesting nonlinear outcomes in dynamical systems that include them. None of this, however, is motivated by, or seriously addresses, niche relationships between coexisting species. The effects of stochastic local extinction on niche similarity of coexisting species have in effect been investigated by Dave Tilman and Schwilk and Ackerly, but I do not think they were influenced by the last sentence of my paper.
HS: Have you ever read this paper after it was published? If yes, in what context?
PC: I am constantly going back to it see if I actually spat out clearly some point that I know I had in mind at the time, so I can refer to it. I sometimes consult the paper when I see a strange citation of it, to see how the citing author could possibly have got that idea. I do not recall having read the whole thing through though, after I returned the proofs.
HS: Would you count this paper as one of your favourites, among all the papers you have published?
PC: Yes, I would count it as a favorite. I like it because it “says it like it is” without worrying about what reviewers might think. It seems to have communicated effectively, and I am proud of it.
HS: What would you say to a student who is about to read this paper today? What should he or she take away from this paper written 16 years ago? Would you add any caveats?
PC: The main thing I would say to a student today is, don’t just read it, make sure you understand why it comes to those conclusions. I would then refer them to updates. But really, the paper is aging well.
In a paper in Nature in 1992, Peter Berthold, Andreas Helbig, Gabriele Mohr and Ulrich Querner provided experimental evidence to show that central European blackcaps (Sylvia atricapilla) had evolved a new winter migration route, and established a new winter home over 1000 km away from their old one, in less than 30 years. Twenty-four years after the paper was published, I spoke to Peter Berthold about the making of this study and what we have learnt since then about the migratory behaviour of this species.
(Interview conducted via Skype on 27th July 2016)
Citation: Berthold, P., Helbig, A. J., Mohr, G., & Querner, U. (1992). Rapid microevolution of migratory behaviour in a wild bird species. Nature 360: 668-670.
Hari Sridhar: At the time when you published this paper, in 1992, you had already done a lot of work on migration, especially on blackcaps. What got you interested in the work presented in this paper?
Peter Berthold: We were really astonished by how rapidly changes in migratory behaviour can occur. When I was a student, I had learnt that, say, for changing a migratory direction or migration time by a week or so would take hundreds, if not thousands or tens of thousands, of years. And some people even doubted whether, after the Ice Age, any novel development of migration in Europe could have occurred. So of course, in the first instance, we couldn’t believe that within, let’s say a few decades, birds could change their migratory direction from a hitherto south-south-westerly-south-easterly direction to northwest, to England. This was baffling for all of us. And also for geneticists to whom I had spoken about it. This was the main reason to publish it.
HS: This paper has four authors. Could you tell us how this group came together and what each person brought to this study?
PB: Andreas Helbig was a PhD student, Ulrich Querner, at that time, was one of my main technical assistants, and Gabriele Mohr was also a technical assistant.
HS: Was Andreas Helbig your PhD student?
PB: Oh yes, he was in my lab and also in the laboratory of Wolfgang Wiltschko. You may have heard about the name Wiltschko. They are a scientist couple living in Frankfurt who have been the leading authorities on orientation research for a long time in Germany. Wolfgang Wiltschko discovered magnetic orientation in birds.
HS: Did Helbig continue in a career in research after his PhD?
PB: Yes, for a number of years, but then, unfortunately, he died of cancer. It was very sad.
HS: I’m sorry to hear that.
HS: In your paper you say you transported these birds back from Britain to Germany to do the experiments. Can you tell us a little about how you actually did this?
PB: This is as we have always done this – they were trapped with mist-nets and then put in small cages. There is a critical time in the beginning, especially on the first day, when you need to make sure that the birds will take food in the cage because otherwise they will die. Therefore, we have developed very specific methods to do this. The rest is very easy – to take them into a car, or from other countries, even by plane. This is something we had developed in our institute in a unique way. In this respect, we have been the world champions.
HS: How long did it take to drive from Britain to Germany?
PB: Less than a day.
HS: Did Andreas Helbig do most of the experiments?
PB: The experiments were run in a large group of people, including many technical assistants. The scientific investigations we did together, step by step. I would say it was split about 50-50.
HS: I want to find out a little more about the sites in Britain where you trapped blackcaps. You acknowledge a couple of agencies for permissions. At that time, was it difficult to get permits to move birds from one country to another?
PB: [Laughs] Not on principle. But of course, you know how it is with Britain, you have belonged to Britain for a long time. In most countries it was very easy to get permissions to take birds – France, Spain, Portugal etc. But the British, they say – Oh, these are our birds, and we normally don’t give permits. So we told them – Listen, these birds that we would like to take from Britain are birds from Europe. They come only to winter with you. They are very bad continental intruders, and you should be happy about every bird that’s leaving England a little bit earlier than normal. You should be grateful to us for taking these food robbers from the British islands back to the continent. Then they said – Oh yes, of course, you will certainly have the permits to take these birds away.
HS: How did you pick the site in England – near Western-super-Mare – to trap the blackcaps for this study?
PB: This was an area in southern Britain, and we had two reasons to trap here. First, this was an area which had one of the highest densities of wintering birds from continental Europe. And second, this is an area with a lot of traps in the dunes, where it’s easy to post mist nets and drive the birds. The British people are very critical about mist-netting, and don’t allow it in their house gardens. In mid-England we have faced a lot of difficulties. But in these coastal areas it was very easy. So let’s say we had chosen the area for good practical reasons.
HS: In the paper, you say you used a “modified Emlen technique” for the migration direction experiments. Can you tell us what the modification you made was?
PB: You know, Emlen used these funnels and inkpads on the ground. The birds would sit on ink pads and when they try to leave the cage they produced these footprints on a white paper. In our technique, developed by Wiltschko and Helbig, we used rubber paper on which the feet, and especially the nails or claws, produce small scratches. These scratches are much more easily counted and investigated. For analysing all these scratches we have developed a specific computer program, which would take all the papers with the scratches and calculate the mean value of the direction and other necessary statistical values.
HS: Is migration still studied with similar apparatus?
PB: I think it’s rarely used now. The Wiltschko group continues to fit the data by eye. Now, in Germany, we have no other institute that’s really doing orientation research with songbirds. Only with larger species. In America they continue to use Emlen’s method.
HS: Have you gone back to the site in UK where you trapped birds, since you did this study? Do you know what the status of the site is?
PB: The site is the same as it was then. It is a protected area. But, of course, with climate warming, there will be changes!
HS: Have the blackcap numbers changed in this site?
PB: They have increased, and are still increasing. This development, started during my time there and is still going on. Now we have blackcaps wintering not only in Great Britain, Scotland and Ireland but also in southern Norway up to Finland. So the whole north is now a large, more or less closed, wintering area of blackcaps coming from continental Europe.
HS: Has this increase been documented systematically?
PB: It has been studied systematically by the British people. It’s quite easy because all British blackcaps are leave the breeding area during winter, and so the blackcaps you observe wintering in England are all from the continent. And the bird counts in Britain, as you know, are, by far, the best in the world. They count every individual.
HS: Do the outdoors aviaries that you used during these experiments still exist? Are they still used for experiments today?
PB: Yes, they exist, but they have been changed. They have been enlarged. I’m retired for about 10 years now, and my successors no longer work with blackcaps. They work with blackbirds – Turdus merula – and the blackbird is, of course, a larger bird than the blackcap, and so the aviaries have been enlarged. What we used to called blackcap city is now blackbird city!
HS: Who did most of the writing for this paper and how long did it take?
PB: It was written by Helbig and me. Writing itself was very easy. It was done in three days or so. What took time was running the experiments – doing the orientation experiments took time, and the statistics to some extent. Once you are at the stage where you can start writing, it is very easy after that.
HS: Were the other two authors also involved in the writing?
PB: No, they were only involved in running the experiment and compiling the raw data.
HS: How did the writing actually happen – would you and Helbig sit together and work, or would you share drafts on a computer?
PB: At that time we didn’t use the computer. Till today, I do all my writing, even of books, by first hand-writing, then by dictating and getting it typed into a computer. Still in the very old fashion way.
HS: So you would sit and write it together?
PB: No, we would each sit each somewhere in a corner and write, and then come together and exchange what we have written. It doesn’t really work to sit at a table and do it in a combined way. That way you talk about everything but science!
HS: How were the figures in this paper drawn?
PB: They were hand drawn, just on a sheet of paper. The orientation figures, as I already mentioned, were made by a computer from the very beginning. The computer did all the analysing and also the printing.
HS: In the paper you thank C. Mead, G. Pudney and T. Parsons. Could you tell us who these people were and how they helped?
PB: They were all people from England. Mead was the head of the ringing office of the British Trust for Ornithology (BTO) in England. He was a good friend of mine and we asked him to help us get the permission to trap. The other two were ringers of the BTO, who helped us trap birds in the field.
HS: You also thank someone by the name of H. Dingle for comments.
PB: Yes, Hugh Dingle. He is an American. He was and still is working in the University of Davis. Hugh Dingle is a very famous investigator on birds and insects. He has written an interesting book on bird migration, as I have done, but his main focus was on partial migration. I had invited him to come to Germany, to stay here in my institute, as a Humboldt Research Prize winner, for half a year. This was a very fruitful time during which we discussed all aspects of the genetics of bird migration. And he also gave a lot of input into this specific paper.
HS: Did this paper have a relatively smooth ride through peer-review?
PB: Oh yes. It was very easy. We got a few very small comments. The reviewers were really enthusiastic about the paper, and so it ran through.
HS: And Nature was the first place you submitted this to?
PB: Oh yes, of course.
HS: How was this paper received at the time it was published? Did it get a lot of attention?
PB: Oh yes. All over the world. And, of course, also in the Max Planck Society. In the meantime we have published a number of papers that are very similar in their content. But this was something like a small revolution, because of the idea of how rapid and how quickly and how efficiently micro-evolution, and therefore evolution as a whole, can work in the living world.
HS: What impact did this paper have on your future research itself? Did it open up new lines of investigation?
PB: This was a milestone in our own research. Following this, we thought about many aspects that could be followed up and that led to a whole series. It finally led to a totally novel theory on avian migration. We found that it was possible, through selection, to make birds from a partially migratory blackcap population from southern France either exclusive migrants or exclusive non-migrants within a few generations. Just in about 5-6 generations. Then the discussions with Hugh Dingle really showed us that partial migration is, in fact, a common habit in all kinds of animals and even plants. From the oldest pre-Cambrian bacteria up to humans, you have partial migration. Wherever you look around partial migration is there. This is probably a habit as common as, let’s say, circadian rhythmicity in plants and animals. Then we looked carefully into the literature on the world’s bird species – now about 10,000 – and found that in more than 80% there is some evidence for partial migration. And even among the remaining, some proportion might be migration. Take the house sparrow. As you know, house sparrows are normally resident, but if you look carefully at them – like it has been done by Professor Parkin in England – about 1-2% of the birds are migratory. It’s a small amount, but still. So even one of the most typically resident bird species all over the world is a partial migrant. Based on all this evidence we developed the theory that partial migration is a basic equipment of all living avian species. Therefore it would be very easy for birds to adapt to all kinds of environmental changes, whether ice ages or climate warming, because even a species like the house sparrow could easily develop in 10-20-50-100 years a fully migratory population, if conditions at home become unfavourable. Or the other way around – a population of barn swallows, now a migrant in Europe, could develop, in about 40 years or 25 generations, a totally resident population, something that I think we will have in the next 50 years or so. All this was initiated by the paper in Nature at that time.
HS: Its now 24 years since this paper was published. Would you say that the major conclusions from this paper still hold true, more-or-less?
PB: [Laughs] No, it doesn’t only hold true; it has become, let’s say, a common sense. At that time we wrote that this maybe a unique rapid micro-evolutionary process that we have observed. Since then we have come to learn from many other papers, many other plants and animals, that this is not an exception. This is normal. But it was absolutely overlooked before we did this experiment. You may have heard about Peter and Rosemary Grant from America, from the Princeton University. They have worked for decades on the Galapagos Islands. They were astonished when, once, after a big drought, a specific population of ground finches went almost extinct, but after a while started to not only survive but also to increase the population again. This was due to the fact that they had developed, in a very short time, extremely strong beaks with which they could open the only seeds that could be harvested in the extreme drought. And when the normal climatic conditions came back to the Galapagos the size of the bill was again reduced to normal size. All this happened within about 10 generations. We have so many more examples – e.g. snakes that lay one more egg in a clutch and so on. And all this can happen within a few generations, in about 10 years or so. So this is now a general biological aspect. Therefore, I would say, the paper opened an area of understanding of how rapid and effective evolution can work everywhere in the world.
HS: If you were to redo this experiment today, would you change anything, given the developments in technology, theory and statistical techniques?
PB: No, certainly not. The only way to show this was to do some breeding and selection experiments. That was the only way. Today, in parallel, we would also look in detail for the genetic structure of the individual birds, i.e. for the genes itself. This is, of course, very very difficult way in birds, but we have managed to do this. We have also found at least one gene now that’s responsible for at least some aspects of migration. That’s something we would do in addition, but the rest would be done as before. There’s no other way around.
HS: And you would still use the modified Emlen funnel?
PB: Oh yes. That is the best way you can do it. There’s nothing better in the world.
HS: In the paper you flagged a few topics about which not much was known, and which you felt needed to be researched further. One of these is the genetic basis of this migratory evolution. Do we know more about that now?
PB: No, this is still not possible. Because you see, while you can easily find differences in the genomes of different species, between populations you find only very very slight differences. You have no idea to what they are really related. So it will be some more decades before that will be possible.
HS: You say “Overall mean directions suggest a breeding origin between Belgium and central Germany”. Do we now know, with more certainty, where these birds wintering in Britain come from?
PB: Oh yeah, we know now. There have been many more ringing recoveries, and many other investigations, based on which we can say this is an area that roughly goes from the south, from Switzerland and Austria, up to Vienna in east Austria, and then up to about almost the whole Germany, up to the area of Hamburg and east Germany. This is the big patch from where the birds that nowadays migrate to England are coming.
HS: Do we also know more about why this change in migratory direction happened?
PB: Yes. We must distinguish between the mechanism that has started this development, which was of course chance, and what maintains it. There is a lot of genetic variation and, by chance, some birds extended the westerly migratory direction to this slightly northern direction, and so by chance they reached England. If England would not have existed they would have gone into the Atlantic Ocean and the story would have ended. But fortunately there was England. And then the birds that entered England had, let’s say, a funny experience – a wonderful land, a mild winter, not so many birds in the winter, in comparison to Spain or France where so many birds from northern Europe were wintering. It was a paradise and therefore, of course, there was a strong selection pressure to increase the number of birds coming there. Now this work has been investigated in further detail. We had already, in our paper in Nature, the idea that this direction change could be accelerated by, so called, assortative mating. We knew already that birds wintering in Britain migrate back to the continent relatively earlier in the breeding season. Also the distance is relatively short. We have followed this up in more detail. We have looked in continental Europe for the very first breeding pairs of blackcaps. From these birds we have taken small amount from the claws, because the claws are growing in the wintering area, and in these claws must be stable isotopes that show exactly where the birds have been wintering. By this method we have found that the very first broods in central Europe are, more than expected, from parents that have both wintered in England. This means that, through assortative mating, there is an acceleration of the new migratory direction development. This has been published in a paper in Science in October 2005. The first author is Stuart Bearhop. In this we showed that there is a high selective advantage. The birds that winter in Britain come relatively early to Germany, choose the best habitats, mate assortatively, and have the possibility of having more than one brood. This is, I think, the main selection force behind the rapid development of these new migratory habits.
HS: Towards the end of the paper you say “Year-round residency has not yet evolved in British breeding blackcaps, but this may be only a matter of time”. Are there any indications that this is happening now?
PB: Oh yes. This will, of course, come in, sooner or later, due to climate warming. Experimentally, we have already shown that this can happen very easily. There was another paper from us in PNAS where we have shown that, in the blackcap, the genetic control of the migratory distance and the amount of migratoriness in partially migratory populations are controlled by one and the same genetic mechanism. So when a population is migrating shorter and shorter distances, due to climate warming, the number of resident individuals automatically increases. We have shown this in a very nice experiment. We took birds from an exclusively migratory population of blackcaps, in this case from south of Germany, and from these, chose the 30% with the lowest amount of migratory activity, i.e. the 30% with the shortest migratory distance. These birds we have selected for lower and lower amounts of migratory activity. In this way, after 4 or 5 years, we had the first 10% of non-migratory individuals from a hitherto fully migratory population. And from this we could calculate how long it would take for a totally migratory population, by directed selection, to convert to a non-migratory population. We found that would be about 40 years or 25 generations. And this is something that will happen in many many bird species during the next 100 years or so. You can read more about this in two places – one is my bird migration book – the English version that has been published by Oxford University Press. And then there is a paper in Advances in the Study of Behaviour where I have summarised all the genetic investigations that we have made in the blackcap. This was in 2003.
HS: Do you continue to work on this topic even today?
PB: No, this is absolutely impossible. I have given this up on retirement, because for this you really need a large institute and a large group of people. Now, I’m totally engaged in conservation issues and totally different things.
HS: Have you ever read this paper after it was published?
PB: I think I have read it a few times, when I was writing reviews on bird migration or when I had to write a new edition of my migration book – in German, it’s now in its 7th edition. Then, of course I go back into original papers. Sometimes, I also go back to it to see the wordings I used to deal with sophisticated concepts or ideas.
HS: When you compare this paper to those you write today do you notice any striking differences?
PB: No, the style has been about the same. I have been writing every week so there hasn’t been much change. The brain is still working to some extent.
HS: This paper has been cited over 300 times. Would you know what it is mostly cited for?
PB: No, I never have looked for citation index. This has never been, for me, of any interest. I was convinced that this was an important paper and that, sooner or later, it will be noticed. Citation indexes are very modern instruments and in many cases absolutely useless. We have had endless discussion in the Max Planck society about how to handle this. This is of no interest for me.
HS: Would you count this as one of your favourites, among all the papers you have written?
PB: Oh yes, absolutely. This is certainly one of the five best papers we have made.
HS: What would you say to a student who is about to read this paper today? What should he or she take away from this paper?
PB: I think the most important thing is that if you have a good idea, and if in coming to a solution you have a lot of difficulties, like we had – to get the birds from England, to take them over, to run long-term experiments and so on – do not give up and keep going. Because in the end you will either be happy to have excellent results or will anyway face many other problems but without any good results. So I think you should not hesitate to choose the hard way.