In a paper published in Ecography in 1995, Carsten Rahbek critically examined the evidence for what was then believed to be a general pattern: species richness reduces with increasing altitude. Rahbek showed that through a process of “citation inbreeding” evidence from just a few studies had become established as a general pattern of biogeography. Rahbek then demonstrated, through a quantitative synthesis of the literature and careful probing of the methods, that, while the overall pattern is one of decline in richness with altitude, there was substantial variation in the shape of the pattern for different taxa and based on geography. Twenty-one years after the paper was published, I spoke to Carsten Rahbek about his motivation to carry out this study, his memories of putting together the literature and doing the analyses, and what we have learnt since about the richness-altitude relationship.
Citation: Rahbek, C. (1995). The elevational gradient of species richness: a uniform pattern?. Ecography, 18(2), 200-205.
Date of interview: 8th August 2016 (via Skype)
Hari Sridhar: I wanted to start by asking you what your specific motivation to write this paper was. It is somewhat unusual, that the first paper of a PhD student has changed the field so dramatically.
Carsten Rahbek: When I was an undergraduate student I got the chance to go on an ornithological expedition to the Andes in Ecuador, the purpose of which was, basically, to do a survey of all the cloud forests. At that time, I became interested in questions that we now call Macroecology. I read a lot of the literature of people like John Terborgh and Jim Brown, and since we were working in mountains, I particularly read everything I could about mountains and diversity patterns. The literature was unanimous that it was a universal rule that species richness declined with altitude. So,with this background, we went on these expeditions.We basically spent 6 months in pouring rain in the cloud forest.It was fabulous; the diversity around us was just astonishing.
When we were done with that – this was way back in the time of no emails –we posted a snail mail back to our supervisor in Copenhagen. We were four people in this expedition, and in our mail we said that since we had now worked six months, would it be okay if we stayed on and made a venture down in the Amazon. At that time, the Amazon was thought of as the richest place on earth and we really wanted to see it. We waited and a month later we got a reply saying – Yes, we could go down to the Amazon.We went down and I have never been so disappointed in my life! I expected to see so many more bird species than I saw in the cloud forest,but there were fewer. I was shocked because everything I read and all the textbooks told me that I should find more species in the lowland. So I started to think about what was wrong – Was it very unusual? Was it because we couldn’t find the species? – this was kind of simmering in my head while I was doing my Master’s degree on other things.
Then I was lucky to get an exchange scholarship to go to University of Wisconsin where I had the great fortune of meeting Michael Rosenzweig who was doing his sabbatical at Wisconsin, writing his very famous 1995 book on diversity. I started, at that time, an independent project where I compiled information about the altitudinal range of all South American birds. At that time there wasn’t a lot of information available – almost no field guides, so it was hard. So I went to Michael and showed him some preliminary results, and he was shocked, because it was everything that it shouldn’t be. But he also was incredibly encouraging, not dismissing it, but encouraging me to continue it. I had a fantastic interaction with Michael. He was working on his idea that species richness did not peak where productivity was highest. Since the productivity level in the lowland was thought to be the highest, my pattern kind of fit well with the new idea he was promoting. I guess that was one of the reasons he was so excited about it. He was enormously keen to start using it, with my acceptance, in his argument.
I kind of knew that I had something that was fantastic but the quality of the data that I had compiled was really bad. I was concerned that my result might just reflect wrong data or bad data. So I decided to spend more time compiling the best available data at that time.This is one of the features of the way I do science. It is not about speed. The other problem that I faced was that, apart from Michael, nobody else who I talked to believed in what I had. I finished my master’s degree and wrote a grant proposal to pursue an independent PhD thesis on this topic. I was lucky to get a Fulbright scholarship to go to Smithsonian and work with Gary Graves. Again, I had never met Gary, it was all over snail mail – I asked him if I could come and he said yes; times were different back then. Gary, who had enormous natural history knowledge and field experience in the Andes was not that surprised by what I found. With his guidance I started collecting high quality data from all the primary literature on this. I first started doing an analytical paper. One of the things I noticed was that when you are working on the slope there is almost no area available in the lowland then the area available was enormous. I started focusing on the species-area effect and trying to factor that out. It took two and a half years to compile my data. At the same time, I wondered why the literature said something else. I reread all the literature, and found out that all the textbooks – MacArthur and Jim Brown and others – they were all citing the same three papers. When I read those original papers very carefully I was shocked to find that the papers told a different story.
One paper was about the Himalayas in which a botanist had plant data only from 3000 m upwards. For the lower part of the gradient he had taken data from Malaysia. Putting these two datasets together he had found a monotonic decline in plant richness with altitude, adding the caution that the lowland data is from Malaysia. But if you look at the textbook versions of this graph they don’t mention that the data come from two different places. Another paper was by John Terborgh on a gradient in Peru called the Vileabamba gradient.This paper is often cited for being kind of the empirical proof that we have a monotonic decline. But most of the paper was about how Terborgh couldn’t find it! He did find the pattern, but also said that they had surveyed mostly in the lowland, and maybe that is the reason.The species richness in the Andes is so enormous that you just don’t find everything. When he standardised his data for effort his monotonic decline turned into a hump-shaped pattern. But then Terborgh said- this is an abnormal situation; it has to be the other way! So everybody cites that paper only for the first part, the un-standardized result.The final paper was by an Australian called Kikkawa. That was a very short paper and was cited in most of the textbooks [Kikkawa & Williams (1971), Search 2:64-65]. I could not find it in any library in Europe. Wisconsin at that time was famous for having the most comprehensive library in the US, but even they didn’t have it. I started wondering how this paper could be cited by so many people,when it was so difficult to find. Finally, I went to the Library of Congress in Washington DC and found the paper. It turned out to be about a page-long with some quickly compiled figures that were probably made in this fashion – here is a field guide, wouldn’t it be fun to compile this figure and plot it?Yes, it showed a monotonic decline but there was nothing in the paper.
So it was just these three papers, and none of them really supported this supposedly universal pattern. At the same time, Michael was publishing his book and he told me – You need to publish, so that I can cite it. I said that I want to be sure. If you read his book, you will notice that he cites a lot of personal communication with me. He was very nice in the way he gave me credit all the way through. It was nice that I had this enormous positive experience with scholarship and how to behave among scientists so early in my career. I finished my analytical paper which was published in the American Naturalist in 1997, in which I show that there is a monotonic decline, but it is mainly caused by an area effect.If you standardise for area, the pattern is hump-shaped. Similar to what Terborgh had found when he standardised for sampling effort. But wherever I showed that result it was just dismissed. People felt it just cannot be true; it had to be wrong. I even had a friendly review where the reviewer said in the margin: my BS meter is ticking. Near the results section he had noted in the margin :my BS metre has exploded.There were no more comments after that. I wasn’t that good in English and so I asked Gary what BS means. He told me it was the b******* metre.
This was the attitude to my result. Nobody believed it. This is actually why I ended up doing the Ecography paper. At that time I read all the literature, and most of the literature did not support the text books or the general belief. Therefore, in order to make way for my larger analytical paper, I decided to do this qualitative review just to prove that my results were not that abnormal. That is what turned into the Ecography paper. When that came out it received very nice review. Ecography at that time was a tiny journal, but this paper opened up the topic in a way that allowed me to submit my large analytical paper. As a result, I had a tremendously good experience with the review system. Rob Colwell was one of the reviewers. He was incredibly thorough and critical but very constructive and open-minded. I had a reviewer who disliked my methods because they were new. If you read Rosenzweig’s book you will see he is arguing that the way I do things is the way forward.
I also had Mike Rosenzweig as a reviewer. That’s an interesting story. As I mentioned earlier, Michael used my results to argue for his hump-shaped pattern in productivity. But in the end of my American Naturalist paper I point out that my data cannot be used to say that because it is very likely that productivity is not highest in the lowland, but actually up in the mountain, because of cloud stripping of water. But at that time there was almost no productivity data available, so everyone just assumed that as temperature declines, productivity declines. I made a huge argument that my data could not be used as the proof of Mike Rosenzweig’s idea. I will never forget Mike’s review comment on this. He was critical, critical, critical and then constructive. He said he disagreed with my interpretation but that I had earned the right to have my opinion. Considering that I was taking the air out of his argument, I thought that was incredibly scholarly of him.
These two papers, and a third one, constituted my PHD. I remember when I was examined for my PhD by a British scientist, he was not very willing to give me the PhD degree because my thesis was too thin!. I think those two papers have made an impact, and the work behind it was many years and high quality data. I use this story to emphasize that it is important as a scientist to be critical about what we think we know. The other aspect it underlines is the importance of natural history. If I had not spend so much time in the field and had this experience that things didn’t match what I read in the literature, I wouldn’t have gone through so many years of effort to document it. That is the background and history to this paper.
HS: It is a fascinating story. Just to make sure I understood correctly: were Rosenzweig and Colwell reviewers on the Ecography paper or the American Naturalist paper?
CR: The American Naturalist paper. I don’t know who the reviewers on the Ecography paper were.
HS: In response to the earlier question, you mentioned three papers that are cited as examples of a uniform pattern in Species richness. Two of these papers – Terborgh and Kikkawa – are cited in your paper. Could you tell us a little more about the third one?
CR: That is a paper by an author called Yoda [Yoda (1967), Journal of the College of Art and Science Chiba University, 5: 99-140]. I might not have used it in the Ecography paper. Many biogeographical textbooks used these three papers, often plotted in the same graph, as proof of the universal pattern. In Yoda’s paper, the dots forming the monotonic decline were not all from the same area. The lowland plots were from Malaysia, which is one of the hotspots in tropical tree species Diversity. It was pretty weird to plot those on the Himalayan plot but you don’t find that information in the textbook. In my Ecography paper, I had coined a term that, at that time, I was very proud about but nobody picked it up: citation inbreeding. We keep citing the same papers, nobody goes back and checks what the original papers actually said, and from that we actually establish a general belief.
The other way in which we establish a general unconfirmed belief is from first principles. If you just believe that everything is governed by temperature, it is a physical reality that the molecules become thinner, and therefore temperature decreases with altitude. Therefore, from a primary level mechanism, you can argue that this is the pattern. This is what Robert MacArthur did. He said we should expect this pattern from first principle, and then he points to these examples and says – indeed we find it. But as I showed in my Ecography paper most of the literature did not support the pattern. What’s interesting is that a number of papers I cite are not in English. I spent an enormous amount of time, especially search the French and Russian scientific literature, to get all the examples that I could find on this pattern. Back then science was published in many different languages but there was this tendency to mostly cite within the literature published from the US and UK. But surprisingly even lot of the UK surveys in Southeast Asia done by the Natural History Museum show a hump-shaped pattern.
HS: Just to help me get the timeline right: What you showed Rosenzweig was the data on range sizes of birds?
CR: What I showed Rosenzweig was data extracted from a couple of monographs. That is the graph that goes into my Ecography paper. No sorry, that was the data that went into Rosenzweig’s book. My ’95 paper was done on a better database.
HS: And you showed the data to Rosenzweig in 1992?
CR: Yes. I did many months of fieldwork between ’89 and ’91, during which I spent a lot of time thinking about it. Then I started compiling the whole thing. I went to Wisconsin in ’90 for a year, and that’s when I started to work with Mike. After that, I spent 3 years compiling a new high quality dataset and I finished it when I was doing my PhD in the S.
HS: You mentioned that, in Terborgh’s paper, he mentions that unequal sampling effort along the gradient could be the reason why he got a monotonic decline. What about the explanation in terms of area? Do you remember when you started thinking about the role of area in causing this pattern?
CR: That was in the field, when I went down to the Amazon. Our experience from the cloud forest was that if one moved five km, there is an enormous turnover in species. In the Amazon on the other hand, the turnover was much less, which caused me to think about what later became very popular as beta turnover. You see that discussed a lot in the species-area literature: how to factor in the turnover. Two things are interesting about the species-area curve. One is the species-area effect in itself, but the other is also to be sure that results do not just reflect beta turnover, but also differences in alpha diversity. This is what I used the species-area curve for, to factor that out, to show that at scales of alpha, beta and gamma, the pattern was persistent. This was the part of the paper that Rob Colwell liked a lot.
HS: Did you submit this paper anywhere else before submitting it to the American Naturalist?
CR: No, American Naturalist was my first shot. But I circulated it to colleagues before; I gave talks about my results. There I was, a very young student, speaking poor English at that time, presenting that what was thought to be a general pattern was wrong. Of course, I received a lot of critical comments, but, as I said earlier, the big scientists – Colwell and Rosenzweig and Gary Graves – they were very open-minded about it. They liked that the paper was critical, but they also asked for a lot of evidence. I think that if you come and say that something that is universally believed is wrong, you need to back it up with substantial data that can face the most critical inspection. Because of that reaction, I decided that it would be easier to get my results published if I could first show that my results were not abnormal, that they were actually in line with most of the literature. That’s why I went back and did the Ecography paper where I analysed the pattern for all the data sets in the literature I could find, and showed that, actually, the pattern in most of them was hump-shaped. Suddenly, my own result for South America did not seem that different anymore. My Ecography paper made it easier for me to publish the American Naturalist paper.
HS: Was the comment about the BS meter from a friendly review?
CR: That was from a friendly review. I won’t name the reviewer except to say that he is a good friend today!
HS: How long did it take you to write this paper? When and where did you do most of the writing?
CR: It is a very short paper, but it took me, after I had the data, about a year, at least a year, to write. I am from a generation that didn’t learn very good English. My English was bad, I struggled a lot. I also had a supervisor, Gary Graves, who was incredibly constructive, but wasn’t sitting down and writing my stuff. When I turned in manuscripts to him, I got them back, basically, covered in red! So he was not rewriting it for me but telling me where it was wrong. It was tough learning. I envy a lot of the young people today who are much better at English when they go into the University than I was. But this was not a quick and dirty paper. I wanted it to be convincing, and I was very careful with how I wrote it. I sent it around to many people for comments, because I knew that it would be controversial. Of course, today, with my strengths, it is the kind of paper I could write very quickly. But back then it was a struggle and a learning experience. It was only the second paper I wrote, so it took more than a year. But in general, even now, I spend a lot of time on papers that are mine. I am not quick.
HS: Did you do all the writing when you were at the Natural History museum?
CR: Yes, at the Smithsonian. I got my PhD from Copenhagen because Smithsonian does not award PHD degrees. But I did most of my work at Smithsonian under the supervision of Gary Graves. Back home, I had Jon Fjeldså, who is also a world class Ornithologist with expertise on the Andes, as a guide. The nice thing was that people with field experience, like Gary Graves and Jon Fjeldså, were not as surprised by my findings as those that were working mainly behind a desk.
HS: Could we go over the names of the people you acknowledge to get a sense of who they were and how they helped?
CR: Yes. Jon Lovett is a botanist, who, when I was doing my PHD, did a post doc in Copenhagen. He is now faculty staff in England. He worked in the Eastern Arc mountains in Africa, and was a fabulous field botanist and he collected enormous amount of small-grain size plot data. At that time there weren’t that many people who looked at diversity along gradients, and Jon was one of few that had a lot of field experience.
José Maria Cardoso da Silva was a Brazilian PhD student in Copenhagen together with me. Of course, as we do today, I worked together with other PhD students and we shared our manuscripts. He was immensely constructive and helpful. Like me he believed that we might be young but we don’t necessarily have to trust everything our elderly generation tells us. He was very critical.
Richard Zusi was another curator of birds at the Smithsonian with a scholarly perspective, who encouraged me a lot.
Thurber was a post-doc who I shared an office with. We spent a year talking about each other’s research, which helped a lot.
And finally, Petersen was an American curator at the Museum of Copenhagen.She helped me correct my English in the later stages of the manuscript.
HS: The last sentence of your Acknowledgement is “The complete list of papers which this Forum contribution is based on is available from the author”. That’s somewhat unusual. Can you tell us why you included that line?
CR: At that time, it wasn’t the norm to put that kind of statement in. Today, it would be right? It’s a requirement. But at that time there was no requirement to put that kind of thing in. Also, there weren’t so many of these quantitative analyses in ecology and macroecology. I don’t remember specifically thinking a lot about it except that this was part of my documentation, to show that I was not making this up. I did receive an enormous amount of requests for the papers, and other people have used this as a starting point for their own research later on. Christy McCain does a lot of the same thing on mammals. She came to Copenhagen, got the data, sat down with me and – at that time I was collaborating with a young PhD student – she got all our data to start with, and then she used that to build up her own dataset.
So it has been used a lot. I spent two years compiling it, and one thing that is particularly interesting in it is the non-English literature. I thought I should share it so that it’s used by others.
HS: Actually, I didn’t know that it is the norm these days to make all the papers available when doing a review like this.
CR: It is. At that time, I don’t think there was a norm. But since it was an unusual paper, I thought that I needed to provide access to the documentation, to show that I was not making this up.
HS: Did this paper have an easy ride through peer-review in Ecography?
CR: No, it didn’t. It went through two or three rounds. It had a very supportive editor-in-chief. Basically, the reviewers said – this is important, it needs to be published, but we are going to be critical. They helped improve the paper a lot. I know how tough it is to be rejected – we all get rejected – but my experience with these first papers from my PhD was incredibly scholarly and constructive. The editor of my American naturalist paper was Susan Harrison. It was a very pleasant, very positive, introduction to the system. It’s not always like that.
There is another thing, which I don’t know if you know: I later became editor-in-chief of Ecography, and I spent 10 years taking it up to a high level. I love that journal and I love American Naturalist. I guess most PhD students love the journals by which they get their first papers out.
HS: Which year did you become the editor-in-chief of Ecography?
CR: I think it was 2003. It was a low-rank ecological journal when I joined, but when I left it 10 years later, it was in the top.
HS: I joined my Master’s in 2003, and I remember that during the 2 years of my ‘, Ecography was one journal everyone was talking about.
CR: I think we were ranked between 40 and 50 in ecology when I joined, and when I left it, and even now, I think it is 10 or close to that. It is interesting – my paper was kind of part of the wave that turned into Macroecology. At that time, the more classical journal were kind of refusing that, they were focused on more classical ecology. It is interesting to see that during this time, Ecography emerged as a macroecology journal with a strong bias towards field data, where you can get good papers on field data. During that time, it basically overtook in impact factor, for people who care about that, Oecologia, Oikos, American Naturalist and Ecology. Let us see how it goes in the future. To me it was just a nice ending to it that this journal published my first paper and later on I became the editor-in-chief of it.
HS: You mentioned that it was difficult to publish this kind of work in the conventional ecology journals. Was that the reason behind the starting of many of these journals focused on large-scale patterns such as Ecography, Global Ecology and Biogeography (GAB), Journal of Biogeography, etc.?
CR: Yes. Journal of Biogeography is an old journal, but the others – Ecography, GAB, Diversity and Distributions – were picking up this new wave. In fact, I use this paper now, for my ongoing work talk, to hammer through two-three points:1. Be critical about what we think we know; 2. Natural history matters a lot; it is your best judgement of what is right and wrong. Today, in my centre, when people come to me after having done all the fancy analysis, my standard to evaluate the results is – if you forget about the results and look out of the window, do we believe it? They reply that their results show it. I don’t care. Do we believe this? What is your experience? Does it make sense from what you know about nature? Of course that is a difficult question, if you have never been in nature and never done field work and collections. I think that natural history, like MacArthur and all those guys emphasized in the past, is enormously important.
Because of papers like this and others that came out soon after, it became very fashionable to do quick and dirty compilations and analysis of a lot of data. The history behind this that needs to be emphasized was that it was not done quick and dirty. I think it has stood the test of time because it was done thoroughly. Today, it actually gets cited more than ever. Twenty years after its publication its citation every year, is more than the year before. What I like about my own paper is the thoroughness. As I said earlier,once I had the result, I basically threw it out because I was not satisfied with the data quality. Then I spent two years being absolutely sure that I got the best data possible. I think the problem with a lot of macroecology, which is a problem with other ecological disciplines too, is this quick and dirty approach. I think that is still ongoing, and that is why I use this paper to tell this story, of the importance of natural history and good quality data.
HS: Do you remember if your paper changed in any substantial way, from the first draft you submitted to the final published version?
CR: Results did not change. I basically had the figures and the results. What I changed in it was the way I wrote it. The first draft was written in a very direct, almost postulating, way. All the reviewers, these scholars, basically told me to tone it down. To be more balanced, more neutral. They kept telling me: you have such fantastic results; if you should write it down in a plain scholarly manner you will have a much greater impact than if you yell. I think that was incredibly good advice.
The other thing that took an enormous amount of time was that I was trying to get data on climate along elevational gradients,but nothing existed at the time. I think it was finally four or five lines in the published paper, but I spent so much time on it because I would have loved to connect it with climate data. But nothing existed at that time.
HS: Today, compiling the literature for a study like this is very easy – click of a button. Could you give us a sense of how difficult it was to compile all this literature at that time?
CR: I forget what it was called, but libraries had this huge publication that listed all the literature. What I did was, every time I got a paper, I looked up and found everything that it cited. It was even more difficult because I had to find papers that may not have been on the topic but that had the relevant data. I think I still have my archives of about 3000 hard copies of different papers that went into this. The papers that had useful data were only a couple of hundred, but I had to go through the whole set of 3000 to know that. I remember going to the Royal library in Copenhagen,which is enormous and has a very good collection. Michael Rosenzweig went to Wisconsin when he was writing his book because Wisconsin was famous in the United States for being a very complete library. I went there too. I also went to Smithsonian, and spent an enormous amount of time in the Library of Congress. It took a lot of time because I needed to find everything. Even then, at the end, there were a couple of papers that I could never find.
HS: And at that time you would have had only hard copies of all these papers. You would have had to extract all the relevant information by hand, right?
CR: Yes. When I found a paper I would make a copy. I still have all of them in my office in these old fashion cabinets. I think there are about 3000 papers that come from this study. It is still in there.
HS: A student today would find it difficult to imagine how different it was then.
CR: Yes, those were different times.
HS: Did the paper receive a lot of attention when it was published?
CR: No. Mike Rosenzweig’s book received an enormous amount of attention. But because Mike had two chapters in which he used my work a lot, it brought me some attention – Who is this guy? Where has he come from? And Mike wrote very nice things in the end about the way I did things. When I published this paper, outside of the circles that already knew about the results, I don’t think it was picked up. I think in the beginning it was only read by those who worked in this area, which was not a lot. Then Jim Brown’s book came out, and I followed up with my American Naturalist paper in 1997, which brought attention to my 1995 Ecography paper. Ecography was a small journal at that time, but the American Naturalist paper drew attention to it, and interest started to explode in this paper.
HS: I wanted to ask you about your interaction with Jim Brown. What did he have to say about your work in his book?
CR: His book came out before I had publish ed my stuff. I think it came out in 1995. He had no clue about my work. I never interacted with Jim Brown on this. My interaction with Jim comes much later, and it has never been very close, except that I think we respect each other’s work.
After I did this work, around 2000, the interest in elevational gradients exploded. Lots and lots of people went out and did work, and the reason this stands is that many people found the same thing as I did. It’s not a universal pattern, it is very diverse, but generally, the finding is that it is not a monotonic decline. There are some studies showing it, which are probably true. But there is huge variation. So it caused a lot of interest in the explanation for this gradient and the variation in it.
I was pleasantly surprised when I read this interview with Jim Brown, where he was reflecting upon this. It was nice to see a scientist like Jim, who has written so many textbooks on the topic, reflecting upon this pattern and honestly saying that they were wrong. He too made the points that I stress here: data quality matters. If you put poor quality data in you get poor quality results out. You might get your publication but it won’t stand the test of time.
HS: What kind of impact did this paper have on your career and the future course of research?
CR: It created my career. When I finished my PhD I very quickly had tenure-track offers from the United States. But I went back to Copenhagen and applied for a curator of birds position. I must have had 4-5 papers at that time, while the other people applying for the position had 40-50. This was about a year after my PhD, for a position at the associate professor level. The search committee was heavily divided on whether I should have a position or not. The committee consisted of some external people and a couple of people from Denmark. The interesting thing is that the people from Denmark favoured the candidates with a lot of publications, but the external people – a German guy and a British guy – – No way! You have to go for this guy (me) because of his papers. The quantity doesn’t matter, it is the quality and the impact of it. If you want to have higher potential, you hire this guy. I basically got my job on these papers.
One of the things I often discuss with my PhDs and postdocs is whether we should hire people based on the quantity or benchmark figures. I tell them that I have never hired the person with the largest CV. Often they say, we don’t believe you, but I tell them I know because I’m doing the hiring! I’m always looking for people who have written papers that stand out, because they are more likely to do that in the future. Of course criteria vary from place to place, but I’m sitting in a Centre of Excellence where we are not being judged on the quantity of our production but whether we write papers that make a difference. This paper and the other papers from my PhD built my career very quickly.
HS: When you got your position, did you know right then that you wanted to continue to do research on this topic? Was that clear to you at that stage?
CR: Yes, but my position as curator of birds involved other tasks as well. It involved being head of the Danish bird ringing scheme and establishing a research programme in bird migration, which I did. But at the same time, I continued with my, what we now call, macroecological research, especially on big datasets. While doing my PhD, I started compiling the first high-quality continental distribution dataset. In the mid-90s, I started compiling that for the birds of South America and later for the vertebrates of Africa before anybody else did that. So I had these two areas – my bird migration and basic ornithological research and my macroecological research.
HS: Today, 21 years after the paper was published, would you say that the main conclusions of this paper have been borne out by subsequent research, that they still hold true more-or-less?
CR: Yes. Other people have done the same kind of thing, Christy McCain and others. In 2005, I published a review paper in Ecology Letters on scale in macroecology, using a follow-up on this, with a huge dataset. Later I had a paper in Nature on the consequences of not sampling the complete gradient and how that distorts hypothesis testing. And that was done on all the papers that came in between.The literature on this exploded -when I did this there were about 200 papers and today my guess is there are 1500 papers. And they still show the same general pattern. I also think that the Jim Brown interview where he is kind of saying we thought it was a general pattern and we have learnt it is not, suggests that my main finding still holds. So I think it has stood the test of time and other people who have done similar things have found similar patterns. So yes, the main conclusion still stands.
HS: If you were to redo this study and write this paper today, would you do anything differently?
CR: No, I don’t think so. When you told me that you wanted to do this interview I went back and read it. And it was a pleasant read! I’ve published other papers about which I have felt was the best I could do at the given time, but I would do it differently today. This is not a paper I would do differently. It actually has a lot of the things I do research on right now, 20 years later, and what is considered cutting edge, on source pool and biotic interactions – how small scale biotic interactions impact large-scale patterns. It’s all mentioned in the ’95 paper. So a lot of the things that I thought back then are still what we are doing research on today. That paper also stresses that – of course, it is not my unique thinking – a lot of the things that we do today, which we think is novel, was already done in the ’70s and ’80s, and this is of course reflected in my writing. In the first wave of macroecology it looks like we just forgot the entire history of ecology and reinvented a lot of things. That’s the other thing that I tell a lot of my PhDs and post-docs when they come to me with their results, which is that now we are going to go 20 or 30 years back because this has been done before. And it’s been done very thorough before. There was more time to do things, there was less pressure on quick and dirty publications. So, it was a pleasant reread for me. I hadn’t read it for so many years.
HS: Yes, that is one of the things I wanted to ask you. Have you had the opportunity to read it again, other than before this interview?
CR: Yeah, I probably read it ten years ago. But of course, people here in my centre who work on these topics read it. Sometimes, when I’m saying – well, I said that back then, they say – No, you didn’t. I have to then go back and check. You forget the details right? But I haven’t read it for 10 years.
HS: At the end of your paper you provide some guidelines on how people should do these gradient studies – including the whole gradient, samples should be regularly spaced, and so on. Do you think studies on gradients, today, have adopted these suggestions?
CR: Oh yes, it has improved tremendously. The challenge that day was very little research was done on elevational gradients, with the purpose of looking at elevational gradients. Most of the data back then was done for other purposes. This is why the results were difficult to interpret. This is why I ended up writing this. I know that Rob Colwell had a big project on elevational gradients in Costa Rica. I interact a lot with Rob, he is an enormously smart guy in setting up these things, and we had a discussion about what was needed for these things. I think that the field-based stuff that is being done on elevational gradients is superior quality to back then. And I think that people have learnt lessons from this, and other studies that followed this. So I think the field-based stuff today is high quality. But the same cannot be said of the quantitative meta-analyses. You see a lot of that kind of work where people are compiling and analysing data from gradients that are non-comparable because they differ in how much of the gradient they cover. The approach seems to be – a result is a result, lets include it in our meta-analysis. I had a post-doc. who came to me and said – I want to follow up on this. We did a Nature paper where we looked at a dataset on plants from the Pyrenees.In that we resampled the data using different grain sizes and different spatial extents. We excluded the lower part of the gradient and the higher part and then we related that to testing hypotheses. What we showed is that as soon as you do not have a full gradient, the same data will support the wrong hypothesis. If you don’t have the lowland, you don’t know if it is monotonic decline or hump-shaped. And all the hypothesis, that’s where they divide the water. The other thing we showed was that, throughout the world, human disturbance is most in the lowlands and the highlands. The highland doesn’t matter so much, but the lowland matters. So, in a sense, we showed that disturbance of lowland is a major problem that affects elevational gradient analyses. Subsequently, we also showed that most lowlands are destroyed,and with it are also destroyed the possibilities to look at undisturbed gradients. There are probably 4-5 natural gradients left in the world. Even today, when people do field-based research on elevational gradients, they have trouble finding lowland samples.So they end up doing a plot somewhere else,or doing a plot in a fragmented landscape etc.So we huge problems with this. This is one of the reasons why I wrote my 2005 review paper in which I critique the nonsensical use of meta-analysis in macroecology.
HS: Another point you make is that the parallels drawn between elevational gradients and latitudinal gradients might be inappropriate. Today, what would you have to say about this? Do you think people today are more circumspect in drawing these analogies?
CR: I would say that many ecologists still tend to do it, but it is less among people who work in the field. I followed up with some other papers where I’m much more explicit on why altitudinal gradients and latitudinal gradients are non-comparable. One very simple reason is spatial scale. Latitudinal gradients span thousands of kilometres, whereas an altitudinal gradient is 4-5 km at best. The processes operating at those different scales are not comparable. On the latitudinal gradient, you have climate gradients on a large spatial scale of extent, and on the altitudinal gradient you have it on a very short extent. I have since argued that it is incredibly interesting to look at scale dependencies in processes relating climate to diversity. And there have been a couple of papers out that look at that. One is by a former post-doc, but very few. In the 90s when I had done this, my dream was to make what today we would call a big project ,and that was basically to establish from Tierra del Fuego to Alaska, which are mountain chains all the way through, elevational gradients on the latitudinal gradient. I wanted to have a climate station on each of these gradients. That’s still my dream project, but it will be a mess and it will be costly. You cannot compare results from an altitudinal gradient and a latitudinal gradient, but the combination of those two axes in the same study at multiple sites will, I’m convinced, yield a lot of interesting insight into what determines species richness gradients.
HS: This is a minor point but just out of historical interest: in a couple of places you mention unpublished data – I wanted to know if these were later published as part of other papers. The first place is in the legend to Figure 2.
CR: Yes, so that’s all the data that went into the American Naturalist paper that was published in 1997.
HS: How did you make the figures for this paper?
CR: On one of the first Macs.
HS: Did you use a software to make it?
CR: Yes, I think this was made in a stats programme called Systat, which I don’t think a lot of people use today.
The other thing with this data is that, I compiled all of it, from the literature and museums, and published it. At the same time, there was a huge project led by a person,who has unfortunately passed away, called Ted Parker, who was one of the best neotropical ornithologists. He had compiled a huge dataset on ecological attributes and geographical distributions of neotropical birds. So we joined forces and that way all my data went into his database and I could use the compiled thing. That was published in a book, along with a floppy disk with all the data, by Chicago Press.
HS: The other mention of unpublished data is towards the end of the paper where you say “A negative correlation between species richness and elevation fits well with the general acceptance that the lowland tropical rain forest has the richest biota on Earth (e g. MacArthur 1972, Erwin 1988). Recent research has shown that this may not always be true on a regional scale (South American mammals [Mares 1992], and birds [Rahbek unpubl]).”
Is this also the same data that went into the American Naturalist paper?
CR: Yes. At this time I already had my manuscript for American Naturalist, so I shared it with the reviewer. So they could kind of see that this was in process.
HS: When you read the paper again recently, did you notice any striking differences in the way you wrote then and you write now?
CR: No, not really. Of course, it is quicker today. While writing this paper and my American Naturalist paper, I spent an enormous time getting trained how to write. I think I established my writing style based on these papers. I’m basically writing in the same style today. I might be a little better in English now, but I think the fundamentals, especially with regard to spending a lot of time on accuracy and a lot of time on what you can call “scholarisation” of the paper – getting the right literature – are the same. If you look at this paper, its 1995, but it has lots of citation to literature in the 70s and 80s right. And I think that’s still a characteristic of how I write, that I get this classic literature into it, I acknowledge the science that was actually done way before the current line of research. I think, in general, I have the same writing style. I haven’t reread the paper looking specifically at that, but that would be my guess.
HS: Would you count this paper as one of your favourites, among all the papers you have written?
CR: It’s hard not to love a paper that changed how science looked at things and that made your career.
HS: What would you say to a student who is about to read this paper today? What should he or she takeaway from this paper published over 20 years ago?
CR: That’s a tough one. I think that some of the main messages that are in my paper are all over the literature today. So from that perspective, if you are a student reading it, I don’t think you will be so surprised by it, because you are also reading it in so many other papers today. Of course, the newer papers also have more data and more sophisticated analysis. I think that what a student could take away from this paper is, if they manage to reflect upon the time in which it was published, and then think about what it would take to come up with something that is convincing in print if what you are saying is controversial. Maybe they should also takeaway that there are not a lot of bold statements and postulations that try to self-inflate the novelty of the work. I think a lot of students will read this and say – what’s novel here? That’s because it is not yelling – this is novel, this is controversial. In macroecology, especially, there is this tendency to say everything is novel, everything is fantastic. I think that is something to take away from this paper. I think that if you want to look at how to write good papers that are convincing, look at some of the seminal papers and I bet that almost all of them share the characteristic of being very scholarly with the literature, toned down and not yelling big words.
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