On serendipity in science: an interview with Laurent Keller

keller

(Reposted from the INNGE blog)

At the European Society for Evolutionary Biology (ESEB) conference in Lausanne in August 2015, , at the end of his ESEB presidential address, climbed up on a table and exhorted young scientists not to ignore unexpected results. He said that his most interesting findings had been serendipitous and had happened only because he followed up on unanticipated results. Keller has also written about this in more detail in a . After listening to his talk and reading his paper, I decided to ask him a few questions.

(Interview conducted via Skype on 15th October 2015)

 Hari: In your E.O Wilson award winner’s address in American Naturalist, you say that hypothesis-driven science and the current academic system ‘castrate’ scientific creativity. Why do you think so?

Laurent Keller: I think hypothesis-driven science is fine, but I feel that people are too fixated on that. They are too much into the framework where they have hypotheses and they want to test something particular, and when they get weird results they don’t look at them carefully. They don’t have time to look to them because they have one question, they are granted three years, they have to write a report and they are stressed to do what they promised to do and when there are unusual things they don’t have time to investigate it further. Also they have been taught that things are a particular way in textbooks, and they believe textbooks too easily. Hypothesis-driven science is fine but people should be ready for unusual results and be ready to move from their pet hypothesis to something completely new. Frequently they fail to do so.

H: You mention that scientists lack time. Do you think that what you are suggesting – following up on unexpected results – will be somewhat of a luxury for most scientists today, given the pressures they face?

LK: Yes, because doing this will be useless when people have to write reports for granting agencies. That’s why I feel that granting agencies should place more value on what an applicant has done in the past than what he or she proposes to do. Some people are consistently good at delivering good stuff, so one can continue to give them money. On the other hand, some people are consistently good at promising to do good stuff but never delivering and they should not get money.

H: I would like to talk a little more about this. You say, in your paper, that “much more value should be put on previous achievements than on the proposed work”. Do you worry that this might lead to a “rich get richer, poor remain poor” kind of situation? That it might make it more difficult for young people, without much to show for in terms of previous achievement, to get grants?

LK: No, I don’t think so. I think someone who hasn’t done much in the past, you could give him or her whatever amount of money, and they won’t do very much, basically. And inversely, to those who did well in the past if you give them a bit of money they will continue to do well. I think we should give some money to everybody – it should not be like in the US system where some get a lot of money and others get nothing.  In the Swiss system if you do good science you get money – you are not under stress to get the next grant; if you are really good you are 100% sure to get your next grant. There’s little stress and opportunities for everybody. I think universities should also support their staff with grant money. Like in the US, there should be fewer people – fewer professors -but when they get a position then they should also get some support from the university. Many countries have a strange system where many people get hired but then they are not given the means to do their research, which is ridiculous.

H: You also say that when evaluating grant proposals “originality and creative elements of the work described in a grant application rather than whether the project is feasible” should be valued. Are you suggesting that granting agencies should stop playing safe and encourage work that has great potential but also high risk of failure?

LK: Some grant agencies say they want to do so, e.g. the European Research Council (ERC) says it wants high-risk high-reward type of projects and in the US also that’s true. ERC maybe does it pretty good, but the US system doesn’t do it so good because the probability to get money is so small that any problem in the grant will be seen as negative and grounds for the application to be rejected. In such a situation, if you propose stuff which is unsure there will always be reviewers who will say ‘well, but we don’t know if you can do this stuff’ and of course you don’t get the money. The only hint that you might be able to do that stuff is if you have done it before. So that’s why I think assessing what people have done in the past is by far the best way to get money to good people. Funding agencies do it sometimes but clearly they don’t do it enough.

H: You present three instances where your colleagues and you made interesting findings only because you did not ignore unexpected results which didn’t fit accepted paradigms. Were there any commonalities underlying these instances, apart from your involvement, which made this happen?

LK: No, they were all situations where we had something unusual and did not throw it away. And, of course, all my collaborators were willing to spend the time required to resolve these puzzles. Each took several years and I was lucky to have money to support them – using it from other grants or from the university. In all three cases it was about finding a way to explain weird results and not throwing it away and start a new line of research based on that. I think people should do more of that because I have seen many cases, while reviewing papers for instance, where people had weird data but failed to realise it.

H: And in these cases do you think the main problem is that people don’t have the time to pursue these side paths or…

LK: I think the problem is people not being open-minded to something new or strange. Most people become so used to seeing everything within one particular framework and so when they see something strange which doesn’t fit what they expect, they just throw it away. Originality and creativity is important for good research and I think some people are just better at that, just intrinsically.  And I do think the system could do more to provide space for such people.

H: It seems like you are suggesting that more people should see science as play and maybe have a little more fun with it.

LK: Yes, exactly. Play and art.

H: You say that scientists these days have become too specialised and that is a problem…

LK: I think its fine to be specialized. If you work in an area you need to really know the stuff but you also should venture out of your field – read widely, go to talks on other topics. I see many scientists who don’t do that, who are stuck to their own topic of research and only go to seminars which are close to their research interests. Only creative people can make links between completely different things that give themselves the opportunity to discover something that’s completely new.

 

H: But specialisation and breadth of interest is a trade-off – more of one means less of the other. Do you advocate that scientists should sacrifice a bit of depth and cast their net wider?

LK: Yes, I think so. People should be more open-minded to fields of research other than their own, which may allow them to make a new link which they would not have made otherwise, and maybe then make some important contribution.

H: You start your paper talking about Darwin and say that Darwin’s ideas depended on the huge amount of natural history work that he did. In the current academic system, natural history has gone out of fashion and is looked down upon. Do you think there should be greater emphasis on natural history work?

LK: Yes, I think so. Only through natural history can one find new interesting things to research and new insights into problems. In a bit of the same way, scientists should read a lot in different fields – that is a different kind of natural history, by reading and not by observing in the field. It’s a natural history of what other people have done. For people in evolution and ecology I think going in the field is important to properly understand the biology of your species and design experiments which make sense.

H: The other scientist you mention in the paper is . You say that Hamilton will find it very difficult to get an academic job today, given all the various boxes that a scientists needs to tick. The sense I get from that is that you think there is too much emphasis on scientists being all-rounders – good at not only science, but also at teaching, grant-writing etc. You think there is less and less space for people who are original thinkers but don’t have other qualities required of professional academicians?

LK:  You can see that in our curricula today – students spend lots of time learning to present their work, to present their PhDs in 2 minutes, basically learning to sell themselves – it’s a lot about selling yourself. Today there is too much emphasis on salesmanship and too little on the quality of the product. In a sense that is understandable because there are too many people in the field.  If you have a job opening, today it is common to have over 100 people applying. In such a situation you don’t have much time to evaluate each candidate and therefore you use shortcuts – you just look at their CVs very quickly but you will never read a single paper. You are just looking at what journals the candidate has published in – the journals are making the ranking for us basically. I realise I don’t have a good solution to this problem – I was just recently in a panel looking at 237 applicants for a job. In the first round all we did was to look at the publication lists of candidates, the prestige of the journals and so on.

 

H: You touch upon education in the paper. What changes do you think are needed in teaching to increase scientific creativity among students?

LK: I think students should be encouraged to find out things on their own. Push them to be more critical – make them read textbooks but then present them some data that doesn’t fit what’s in the textbook, so they see that everything they read is not always correct. In my course, when I tell students that 95% of what I teach is correct and 5% maybe wrong they are very unhappy – they say ‘how can the teacher be wrong?’ There is too much emphasis on learning by heart and not enough on creating new things and finding out things yourself.

H: In general, too much emphasis on what’s known rather than what’s unknown?

LK: Yes, exactly so. That is a good way to say it.

H: You have mentored lots of students over the years. What has your mentoring strategy been – have you actively created the conditions to allow what we have been talking about to happen?

LK: Yes, I think so. I just checked yesterday – more than 30 of my students have got permanent positions in universities and 10 of them are still in the academia track somewhere – tenure track type of thing. I believe that, on average, every professor should create at least 1 or 2 replacements for himself.  I believe that my students have been particularly succesful because I just let them do what they want. I help them and guide them a bit, but mostly let them be. So the strategy is really just pushing them to do new things and not stressing them about time. I don’t tell them ‘you have two years’ or ‘deliver a paper by next year’. I much prefer people staying for longer – even 6 years  – to do one strong study and produce one good paper rather than 6 medium quality papers.

H: I also notice that you have done a lot of work in collaboration with a robotics lab. Speaking about collaboration in general – do you think that’s another route to more originality and creativity in science?

LK: Myself, I am going in many directions. I work not only on ants but also on C. elegans and on Drosophila, bacteria and fungi and modelling work. I am not really competent in all these fields so I need to work with students or collaborate with other scientists.  I value collaboration very highly because it allows me to move into new fields I don’t have expertise in, to learn new things and meet new people. For me that’s the fun of science.

H: One last question – can you name some of your favourite papers, or scientists you admire, which exemplify what we have been talking about?

LK: For me, the most impressive are some papers by , I guess. He really did stuff that nobody had thought about, had really creative ideas and, really, after Darwin, he is the most important person in evolutionary biology, I think.

 

H: And among all the pieces of work you have done, is there a favourite?

LK: Well, I like our work on fire ants – – which took us 20 years of work to figure out. I also find quite interesting .

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3 comments

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