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  • Post date: 2 years 1 month ago
    Citation for this post: BibTeX | RIS

    The 8th International Conference on Mycorrhiza was held at the Northern Arizona University in Flagstaff, UWA. It was organised by professors and . This year theme was “Mycorrhizal integration across continents and scales” and it exceeded all expectations. There were presentations regarding all aspects of mycorrhizal fungi, from cultivation of edible mushrooms to global distributions and ecology of mycorrhizal fungi. I might be biased but my favourite presentations by far were the ecological ones. For example, PhD candidate showed what drives ericoid mycorrhizal fungal communities during-long term ecosystem development in Hawaii. He showed how ericoid mycorrhizal diversity increased  and community composition changed with soil development, and this was associated with soil phosphorus.

    An unofficial topic throughout the conference was the use of the term “Giants” to refer to researchers who have dedicated a lifetime into studying mycorrhizal fungi, and several of them were invited to the . Among these giants, presentation by Dr. was among my favourites as he told the story of the beginning of the studies of mycorrhizal fungi and how this knowledge developed through time.

    Grand_canyon

    As a young researcher I found incredibly exciting to have the chance to talk to researchers such as Dr. and Dr. (Editors of New Phytologist and Mycorrhiza, respectively). Also, Dr. Randy Molina hosted a small session for young scientist about submitting and publishing scientific papers, where he explained the process of publication from an editor’s view. This session was very useful and cleared several questions I had. For example, doubts about who to include as co-authors and in what order were cleared.

    The conference also offered an excursion day to the Grand Canyon which was absolutely beautiful. Having the chance to see one of the world’s natural wonders was the cherry on top of an excellent conference.

    Finally, the broad-scope theme of this year really helped me broaden my view of potential future research, as it covered all areas of the study of mycorrhizal fungi. Now, it is very clear that any mechanistic study should take into account potential interactions with other trophic levels of study (e.g. including plants and herbivores into mycorrhizal studies).

  • Post date: 2 years 1 month ago
    Citation for this post: BibTeX | RIS

    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 .

     

     

  • Post date: 2 years 2 months ago
    Citation for this post: BibTeX | RIS

    is an assistant professor in the experimental plant systematics group at University of Amsterdam. Recently, he published a paper titled . After reading the paper, I decided to ask Patrick a few questions about why he wrote this paper, why he thinks these mistakes are so common and what he hopes the paper will do for the field of population genetics.

     

    To whet your appetite for the interview that follows, here are the seven mistakes:

    1. Giving more attention to genotyping than sampling
    2. Failing to perform or report experimental randomization in the laboratory
    3. Equating geopolitical borders with biological borders
    4. Testing significance of clustering output
    5. Only interpreting a single value of k [number of clusters]
    6. Misinterpreting Mantel’s r statistic
    7. Forgetting that only a small portion of the genome will be associated with climate

     (Questions emailed to Patrick on 28th September 2015; Patrick emailed back with his answers on 30th September 2015)

    Hari: What was your motivation to write this paper?

    Patrick: Over the years, I came across many instances where people made mistakes, often quite simple ones, in their population genetic analyses. Some of these I encountered quite often and I always thought I should write a paper about them. However, every single mistake did not carry enough weight to publish by its own, so I decided to put them all together into a single paper.

     

    H: You make the point that the easy availability of large genetic datasets has contributed to this problem. Can you tell us why you think so?

    P: Nowadays, there are a lot of people without any formal population genetic background who use genetic data [also see ]. This is because it is increasingly easy to get genetic data, because so much of the genotyping can be outsourced. On one hand this is great, because a lot of interesting questions that are outside of the realm of classic population genetics can be answered using genetic data. On the other hand this is dangerous because those researchers may not be aware of the limitations of genetic data analysis and the assumptions and biases of the used methods.

     

    H: Your paper lists seven mistakes - are these the most important, according to you? Are there others you have left out of the paper?

    P: I wouldn’t say that my list is exhaustive or that the listed mistakes are the most important ones. These were just several that I thought were worth pointing out, because they had received relatively little attention so far. I would argue that the most important problem in population genetic analyses nowadays stems from the large number of false positives that many methods suffer from (though I do mention that also in the paper). However, that is a problem that has received quite a bit of attention, for example in the great series of papers by Lotterhos & Whitlock [e.g. see ; ]

     

    H: One of the mistakes you discuss is 'Giving more attention to genotyping than to sampling'. You say: 'faced with limited financial resources, researchers often prefer to spend their money on additional genotyping than on sampling. This is unfortunate as a failure to invest in robust sampling may completely waste the investment in genotyping.' Why do you think this is so, i.e. why is sampling given so little importance in genetics studies as compared to, say ecology studies?

    P: To generalise: while the typical ecologist likes to be in the field taking samples, a stereotypical geneticist likes to be in the lab. Sampling takes time, effort and skills, and so does genotyping and data analysis. So there is a trade-off here as well. In ecology, the data collection often starts and ends in the field. So the quality of your data is mostly dependent on your sampling strategy. In population genetics, sampling is only the first of many steps in the data collection.

     

    H: You say that where it is not feasible, one should be willing to 'skip analyses all together'. This is a topic that has been attracted some debate in science  - some people feel that it is better to not do at all rather than do something poorly, while others feel that we should do the best we can, given current knowledge. Are you an advocate of the former?

    P: I am mostly an advocate of the former and I realise that may make my own genotyping papers a bit boring since I do not throw every possible statistical technique at my data. A more nuanced view would be that it definitely depends on whether a method has a large error or whether it has a bias. When it is mostly a question of error, it is no problem to do things poorly, since when taken over many studies the results will be approximately correct. When there is a bias, it is very risky to do things anyway, since when taken over many studies, we will be falsely confident in the wrong direction.

     

    H: Some of the mistakes you highlight, when illustrated with the unicorn examples, seem ridiculously obvious. Yet, they seem to be very commonly made. Why do you think that is?

    P: There may be different reasons for this. One reason may be that people put too much trust in genotyping data. Biologists learn in their first year that every individual has a certain genotype that is unique and will not change throughout its life. So they get the idea that genotypes are fixed and therefore that genetic data represents “the” genotype of an individual. However, it is not; it rather is an estimate of the genotype of the individual, with all kinds of possibilities of error. Once you have accepted that, it is obvious that we need to allow for this in our sampling design, and all other aspects of the genotyping.

    A second reason may that people have trouble with the transition from univariate to multivariate data. I have talked to people about these issues, and often they agreed that the problem was there for univariate data, but somehow thought that it would not be the case for multivariate data. The complexity of multivariate data can be so big that we miss very simple issues. 

     

    H: If I asked you what the 2-3 main takeaways from this paper, what would you say?

    P: The first is to approach genotyping studies really as an experiment. This means that at all steps, one has to keep in mind that there may be biases and therefore one has to take proper precautions for this. Another main takeaway is to make a proper distinction between confirmatory and exploratory analyses, since this really impacts the strength of the inference that you can make. Nowadays these things are often not made explicit, which makes it very difficult to judge the merits of certain conclusions that are derived from population genetic analyses. Finally, start by not believing the outcome of your analyses, as there’s a fair chance that they are wrong. Only accept results after a large amount of scrutiny

     

    H: The entry of modern genomic tools into molecular ecology is fairly recent. Do you think what you describe are teething problems which will go away as the field matures, or do you think a more proactive effort is required?

    P: I mostly positioned the paper in the light of modern genomic tools because they exacerbate the problem because of their sheer size and power. However, many of the problems have been around for a long time. So it is definitely not the case that these are teething problems that will go away. I hope that my paper actually helps to fix this.

    There are other problems that will certainly disappear as technology progresses. For example, the sample sizes that are used for whole-genome analyses are often rather small. Often, only a handful of individuals from a couple of populations are sequenced. These sample sizes are orders of magnitude lower than a typical study that uses microsatellites. This limited sampling introduces a large number of issues, because the demographic and genealogical stochasticity is often so high that this cannot be captured in so few samples. Obviously, this problem will go away very soon as technology proceeds even further.

     

    H: I notice, in your reference list, that there have been a few other papers highlighting problems with population genetics methods (e.g. ; ) . You have also written other papers in the past on this topic (e.g. ). How have these papers been received within the community of population geneticists? Do you think they will have an impact on the issues you are addressing?

    P: I get quite a lot of emails from researchers about these issues, so I think it is being picked up very well. I also often hear from people that they have been specifically asked by the reviewers of their manuscripts to discuss these issues. It is also good to see things change in the literature as well. For example, a couple of years ago, researchers did not seem very much aware that neutral processes like isolation by distance can create patterns that closely match those that result from selection along an environmental gradient. Several papers then came out that commented upon this (including ). Since then it has become standard to take this into account in the analyses, and several new methods have been developed for this.  

     

    H: Can you name a few of your favourite population genetics studies/papers, i.e. which you think are based on appropriate design and analyses and careful interpretation?

    P: There are several studies that I cite in my own paper that I like very much. The is really great. It’s about the population structure of humans, so it’s no surprise that they have excellent genotyping. But what I especially like is the fact that they put an incredible amount of effort in sampling. I also really like the , since it is a great example of how to use simulations in a genotyping study. They realized that there might have been a bias in their analyses, and then used simulations to see whether this was really the case.  

     

     

     

  • Post date: 2 years 2 months ago
    Citation for this post: BibTeX | RIS

    Interview conducted on 28th August 2015. This interview is reposted from .

    holds an undergraduate degree in Electrical Engineering from BMS college of Engineering, Bangalore (1968), a Master’s degree in Electronics from IISc (1970) and a PhD in Engineering and Applied Science from Yale University, USA (1976). Over the last 40 years, he has been studying vision and cognition, primarily in bees, and its applications in machine vision and robotics.  Currently, he is a Professor of Visual Neuroscience at the Queensland Brain Institute in Australia.  On his last visit to Bangalore, I spoke to him about making the transition from engineering to biology, working with bees, how he picks his research questions, scientists he admires, etc. This is the second part of a two-part interview. The first part can be found here:

    Hari: I notice that has received a lot of media attention. How did that discovery happen? Was it also accidental?

    Srini: It was a follow up on the idea that bees can measure the visual flow and integrate that to know how far they have flown. Marie Dacke from the University of Lund, was visiting me as a post-doc and we were wondering about the importance of landmarks along the bee’s route – are they just treated as something that also contributes to the optic flow or are they seen as separate entities? We started to do that, but we were not the first to ask that question - . But it seemed to us that their experiments were not designed with proper controls. Let’s say you train a bee to go and find food after it has passed 3 landmarks, i.e. the 4th landmark is the one that provides the food. To tell if the bees are actually counting landmarks and not just measuring optic flow, you need to change the distances between the landmarks but always ensure that food is at landmark 4. Only if the bee goes to landmark 4 irrespective of the distances between the landmarks, can we rule out optic flow. This was the change we made to the original experiments conducted by Chittka’s group and found that bees can, in fact, count.

    H: 4 is the maximum they can count?
    S: Yes, 4 is the maximum, for some reason!

    H: Earlier, you spoke about how science is driven by publication these days. For people like me, who are at an early stage in a scientific career,  the moment when a paper gets accepted by a journal is a big deal. A big relief. After publishing 100s of papers in your career, do you also feel the same way?
    S: It feels even better to me these days, because it is becoming harder and harder to publish! The competition is getting stiffer and stiffer and so it is even more of a relief and joy, these days, when a paper gets published. Also the feeling that your work gets to see the light of day, hopefully someone will read it and enjoy it. I just wish that this constant emphasis on having to publish in high-impact journals and build up your citation index would gradually go away. I think there are encouraging signs, with the growth of these , where you can deposit something – unrefereed – and people can make their own judgement about whether they like it or not, and even put in commentary. That seems better than this long-winded process of refereeing and rejection and resubmission. It just seems like a lot of waste of time. People who read papers are usually good judges of what they see, and they can decide whether something is good or not, and I think that that’s the way it should be. Storage and space is not an issue any longer with electronic journals, so that is likely to be the way of the future.

    H: If I asked you to pick one or two scientists whose work you really admire, who would they be?
    S: In my own field, I would say my own gurus, I suppose. My PhD professor , who is an engineer-turned-biologist like me, really laid the foundation for me getting interested in insect vision. Then when I went to Australian National University, I worked with this professor called . What was amazing about him was that he really taught me to think laterally. If an experiment did not work he would come up with an interesting theory as to why it did not work and make you pursue another question which will give you an interesting answer to the whole thing. He really was very nimble on his feet. And then when I went to Zurich, there was who has done wonderful work on ant behaviour. I learnt a lot from him, not just about conducting scientific research but also the didactic aspect of it - how to talk about these things and how to communicate these ideas to the public. He was also extremely good at making slides. - not PowerPoint but old-style slides. He would always prepare them in such a way that the main point of the slide was immediately apparent, without a lot of clutter and unnecessary detail.

    H: Among your contemporaries, especially in animal behaviour?
    S: There is this person called from University of Sussex who has studied arthropod vision and behaviour to answer a whole variety of questions. He is such a polymath. Every topic is slightly different but he champions it and writes so beautifully about it. I really admire his work and he inspired me a lot. There is another person, also in Sussex, by the name of , who has done a lot of work in spatial orientation and navigation in bees and ants. I admire their work a lot and have been inspired by it. In the field of biologically inspired robotics, I greatly admire , at the Centre Nationale de la Recherche Scientifique (CNRS) in France, who was the first to build an autonomous terrestrial mobile robot based on the principles of insect vision. Another imaginative scientist/engineer working in this area is at the Ecole Polytechnique Federale de Lausanne in Switzerland, who has used intriguing biological principles to design a large variety of robots, as well as a miniature artificial compound eye that has the same functionality as an insect eye.

    H: I am at the stage where I have to decide whether I want to get into a full-fledged research career or not. One consideration, in that decision, is all the additional responsibilities that come with being a scientist – administrative and managerial responsibilities, grant writing, paper work, being part of committees etc. I am sure at the stage you are in your career, this sort of work takes up most of your time and leaves little for hands-on research. Are these additional responsibilities something you enjoy or do you just put up with them?
    S: I think it is really something I put up with. My ideal would be to just be left alone to do my own hands-on research. That’s what I would really love. But unfortunately the system doesn’t work that way. If you try to do that they will say you are a failure! If I could digress for a moment – some ten years ago I knew a really brilliant mathematics professor called , who happened to be my neighbour. There are even some equations he developed which are named after him - Baxter equations. He is the sort of man who just likes to work by himself. He didn’t need much money, just a notepad and a pencil and time to be left alone. But his university would hound him constantly, asking him to apply for some grant or the other. Rodney would always tell them – 'look, I don’t want it, I don’t need the money, I am happy to be just left alone'. The university didn’t like that. They wanted him to get the money because there is pressure to get money - because the performance of the university is measured by how many grants it gets. So, finally, things came to a head and the university told him if you don’t apply for a grant this year we will deprive you of your office. Rodney said 'fine' and resigned! He retired early and continued to work from home. I would walk by his house every day and we would say 'hello' and I would say ‘what are you doing Rodney?’ and he would say – 'oh, I am just working on some sums' - he had this modest way of saying it. And then later on, two years later, it turned out he won two major awards in mathematics for what he did during that period – no thanks to his university.

    H: You say you don’t enjoy the additional responsibilities that come with being a scientist, but are you good at it?
    S: I am moderately good, I wouldn’t say I am the best. That is one of my shortcomings. My students constantly keep reminding me about deadlines and saying – ‘hey you know, I have my milestone coming up for my thesis, read my project’. That sort of thing happens a lot. I wish I could be a little better with that but I am just not cut out for it, unfortunately.

    H: What about teaching, and guiding PhD students?
    S: I enjoy teaching a lot. I don’t know if the students enjoy my teaching, though! Guiding PhD students is also something I like. In the Australian system it is really the responsibility of the supervisor to make sure the students gets their PhDs. This is unlike the situation in the US, where the student is left alone most of the time to do his or her research. There, the supervisor only points out the general area of research and it is the students who have to come up with the specific ideas. Here, in Australia, it is somewhat different. The supervisor is responsible for how the thesis turns out and even if the student under-performs the supervisor can be held responsible. So, the supervisor has to take an active role in mentoring the student and guiding them at all stages.

    H: A PhD in Australia is typically 3 years?
    S: Yes, and it can be extended to a maximum of 3.5 years, but after that the scholarship stops. If we have some additional money in one of our research grants and the grant is relevant to the project we might be able to find some funds to continue to support the student, but otherwise it becomes very difficult. Of course, there is no course work, so students go straight into their research.

    H: Here (in IISc) students get five years to complete their PhDs (including a year of course work), with the possibility of an additional year at reduced scholarship.
    S: That's wonderful. I wish it was like that in Australia too, because it would produce much better quality theses. In our university, the thesis goes out to examiners in other countries, and so we have to let them know that the work was done only in 3 years and that therefore the quantum of work done needs to be judged in that context. They have to be made aware of this in advance, so that they don’t expect a five year thesis.That’s the situation.

    H: Do you still find the time to do get involved in the experiments?
    S: Not in the doing of the experiments itself, but I help with the formulation of the scientific question, the design of the experiment, the modelling and analysis, and to some extent the writing. Sometimes, if something requires more than a few pairs of hands, I go in and help. I do menial things like feeding the birds in the field site during the weekends - I don’t like to bother my students or staff with this in their off-days so I go and do it myself.

    H: Do you miss doing experiments, observing bees etc.?
    S: When I retire, hopefully, I will get back to that. I can do exactly what I want then.

    H: Speaking of retiring - you turn 67 today, how much longer do you plan to continue at the university?
    S: There is no official retirement age, but I think as you get older the pressure on you gets progressively larger to make room for younger people. It is only fair. If I sit there and consume a big salary it prevents other younger scientists from coming in and being funded for their research. I have some grants which continue for another 2 years. After that I will think of winding down. I am looking forward to that.

    H: If you look back, is there anything you would have done differently? Is there anything you wanted to but were unable to do?
    S: Not really, no. I have been fortunate enough to be able to do whatever I wanted to do. In addition, I unexpectedly happened on things that turned out to be exciting. I really have a lot to be thankful for. No, absolutely no regrets, although I may give that impression because I sound cynical at times.

    H: If I put it slightly differently – if you had to advice somebody, who is early in his research career, what would you say?
    S: My advice would be to try and follow your own heart. Don’t succumb too much to external pressures about what you ought to be doing. Nowadays, the current wave is to relate everything to molecular biology. That sort of thing somehow becomes quite artificial sometimes. You find a lot of people doing molecular biology, even if it is not terribly exciting, because that’s the only way to get published in a particular journal. Try not to do that. Follow your heart. That’s what I always did. I didn’t worry much about whether that would give me a career or long-term job prospect. I did something only if it was interesting and that usually works out best I think. Your heart has to be in it and you have to really enjoy it. That’s what really matters in the end.

    H: What advice would you give on running a lab or research group?
    S: Ideally, if one has the luxury of hiring a lab manager who takes care of all the routine material – making sure the supplies are available, organising things like field trips, taking care of all financial purchasing and payments – that would be terrific. That would mean you would be left alone to focus on the research part, work with students and post-docs to plan the research, and of course retreating from time to time to work on research grants. I used to have this luxury earlier, but that has gradually dwindled away because of shortage of funds. I can’t afford to have a full-time administrator anymore and now I do it mostly by myself. I can still use some of my money to hire somebody but that means I have to cut back on a student, or cut down travel money for students to go to conferences etc., and I don’t want to do that.

    H: You have spent all your research career out of India. Have you ever wondered about how things might have been if you had worked in India instead? Do you think you would have been able to do all that you did?
    S: That’s a good question, though I haven’t given it much thought. I feel that science and teaching in India is extremely creative and imaginative. In fact, some of the best teaching I have had really was in Bangalore at the BMS College of engineering. We had some wonderful teachers and I owe them a lot. And now when I look at the calibre of the PhD students who come and work in our lab, from India – we have recently been fortunate to have a couple – they are very good. Yes, in a way it would have been nice to stay back I suppose but I am thankful for the experiences I got living abroad. Like living in Zurich and learning German. All that cultural exposure I am grateful for.

    H: The reason I ask is the following: there are numerous examples of Indians, like you, who have gone abroad and been remarkably successful in science. At the same time, science done in India receives very little global attention.
    S: I don’t know if it is all to do with quality – a certain amount of prejudice is involved I feel. I often got the feeling that, earlier, any paper that came from the Indian subcontinent was automatically perceived by the referees as being not up to standard, whereas the same thing if it came from a prestigious university in the US or Europe had a much better chance of getting in. That bias has always been there but is gradually going away now I think – people are realising that science done in India and Asia can be very good.

     

  • Post date: 2 years 2 months ago
    Citation for this post: BibTeX | RIS

    Interview conducted on 28th August 2015. This interview is reposted from .

     

    holds an undergraduate degree in Electrical Engineering from BMS college of Engineering, Bangalore (1968), a Master's degree in Electronics from IISc (1970) and a PhD in Engineering and Applied Science from Yale University, USA (1976). Over the last 40 years, he has been studying vision and cognition, primarily in bees, and its applications in machine vision and robotics.  Currently, he is a Professor of Visual Neuroscience at the Queensland Brain Institute in Australia.  On his last visit to Bangalore, I spoke to him about making the transition from engineering to biology, working with bees, how he picks his research questions, scientists he admires, etc. This is the first part of a two-part interview

     

    Hari: To start, I want to ask you about the transition from being an engineer to being a biologist. You are an engineer by training, but most of your research has been in biology. In ecology too - the field I come from - there are quite a few engineers-turned-ecologists, and the general impression I get is that they tend to do particularly well. Do you think your training as an engineer has been an advantage in your career as a biologist?

    Srini: Maybe it has. In my case the transition was completely accidental. I did my undergrad. in electrical engineering at BMS College, Bangalore and my master’s in electronics at the Indian Institute of Science. When the time came to pick a master’s degree research project my professor suggested that rather than do a standard engineering project, why don’t I try my hand at modelling a biological system. So we decided maybe we would try and model the human eye, the way it tracks a moving target, as a feedback control servo-mechanism, which was the kind of thing we were trained to do in the engineering course. It sounded like fun, so I got involved in it and it turned out to be a nice project. Then when the time came to pick a PhD topic at Yale University in the USA, I looked for someone working in the interface between biology and engineering and it turned out that the only person working in this interface area was someone working on insect eyes. So that is how I ended up researching biology, purely by accident. Coming back to your question - it does help to have a bit of a quantitative analytical background to model biological systems, but what we do need to learn as an engineer, from the biologists, is what the interesting questions are - what are the fundamental questions in biology - quite often engineer don’t really grasp that until they have spent a lot of time in that field and that’s the hard part. What sounds exciting to an engineer might not be very interesting to a biologist. So that’s something we have to learn only through experience I think.

     

    H: So are you saying the comfort with numbers helps?

    S: I think so. Going the other way (biology – engineering) might be a little bit harder. As a biologist, if you are not trained a lot in the quantitative disciplines it becomes a bit harder to grasp all of those when you are older.

     

     H: Did the engineering background also help you in doing experiments - working with your hands, fabricating experimental setups etc.?

    S: That’s right. It depends on the nature of the experiment you are conducting of course, but in many of the experiments we do, maybe it is because of the engineering background that we end up designing the experiment in a certain way - building gadgets, using dynamic visual stimuli, or some complicated electro-mechanical device which moves a target or something to see how an aggressive bee chases a moving target, and other setups that require engineering skills.

     

    H: Was picking up the biology difficult?

    S: Not really, no. Fortunately I did not require molecular biology – that would probably have been a lot harder. The sorts of biology I was engaged in – mostly neurobiology - was fairly straight forward, so it wasn’t a problem at all.

     

    H: Did you do courses in biology?

    S: Yes. I went to Yale to do my PhD in the engineering department and I did all my qualifying exams in engineering. But then my supervisor said that it will be good if I also took some courses in neurobiology, to get some basic grounding. So while I was starting my research I took those as well. That helped me a lot.

     

    H: What about beekeeping and working with bees – how did you pick that up?

    S: There again, I was very fortunate. I did my PhD on flies but when I went to Zurich I had to switch to working on bees. There was this amazing lady called Miriam Lehrer - she has passed away now unfortunately – who was the world’s expert in training bees. She taught me how to train bees and observe them. I learnt everything from her and it was an amazing experience. We made a nice team - she was trained as a zoologist and I as an engineer, so we could design and build interesting apparatuses which probably wouldn’t have happened if the two of us hadn’t gotten together. That was a very nice circumstance. Although, I must say, that the experiment we did in my first summer there turned out to be disaster. We wanted to see how rapidly the insect visual system responds to visual stimuli. In humans, we know that that the flicker fusion frequency is 50 hertz – if you present a human with a flickering light of more than 50 flashes per second he can’t distinguish it from a steady light. We wanted to find out what this frequency was for bees. Of course, unlike humans, bees won’t tell you when they stop seeing the flicker, so we needed to design a suitable experiment that would tell us the answer. We gave the bees a steady light on one side and a flickering light on one side, such that the mean intensity of the flickering light of was the same as the steady light, i.e. the only thing different was the flicker. Then we trained bees, with food, to only go to the steady light. Then by gradually increasing the flicker frequency we wanted to find out at what frequency the bee stops distinguishing between the steady and flickering lights. That was the idea. It sounded very good, but no matter what we did the bees just didn’t distinguish between these stimuli. It was very strange, because to you and me, it would have been very clear that the two stimuli were different. And I’m sure the flicker was being registered in the neurons in the bee’s visual system. But the bee as a whole behaved as if it could not tell the difference. Very strange. So we tried that for a whole summer and it was very frustrating. Later, we repeated the experiment, but instead of using just a change in intensity for the flicker, we changed the colour, i.e. the flickering stimulus changed colour to alternate between blue and yellow. That the bees perceived immediately and we found the flicker fusion frequency was 100 Hz. Maybe the bees are not programmed to perceive flicker in intensity. It is probably irrelevant to them. Maybe if I was a biologist I would have known that right away!

     

    H: Something I have always wondered about is the relationship between scientists and their study animals. In most cases, the relationship is purely scientific to start with, but I wonder if that changes over time and some sort of bond develops between scientist and animal. Has that happened with you, with bees?

    S: I didn’t have any particular affinity for bees before I started researching them. As an engineer you don’t even think of animals, which is a pity. It is only after studying bees that I have an appreciation for them. The more I study about them, the more I appreciate how much is going on in their tiny brains, and my sympathy for them grows. They really are wonderful creatures. Thankfully, our experiments do not involved doing any damage to the bees. They are free to come and go as they please and at the end of the experiment they continue their own lives in the hive. They are not sacrificed in any way and I feel very good about that. Except in the recently started pain project, where we are trying to see whether we can obtain some evidence of whether invertebrates perceive pain. In these, we have no choice but to inflict some discomfort on them.

     

    H: Tell us a little about the way you do your research: how do you decide whether a particular idea is worth investigating or not?

    S: One thing I suppose is originality. If it’s an idea that has not been tackled before and looks promising and interesting, even if it does not have an immediate application in engineering, I feel it is worthwhile pursuing. The second factor is how doable it is. One nice thing about working with bees is that they will tell you fairly quickly whether something is going to work or not. You don’t waste time. Typically in a bee experiment, you will learn within 3 or 4 days whether something is going to work or not. And then you can change your plan. So, originality and doability are the primary deciding factors.

    Of course nowadays, we also have all these other pressures that students face when they have to pick research ideas. Often I have students who come to me and say ‘look, I want to do a six month project with you as a part of an undergraduate program.’ When I suggest something, the first thing I get asked is ‘where will I be able to publish a paper on this?’ They want it to be a high-impact journal. So the basic intrinsic interest of the topic is no longer the prime factor. That is a bit disappointing, a bit worrying. But it’s not the student’s fault; I think the system is driving them that way. Look at our PhD students in Australia. They have clearly chalked out plans - by this time I will submit this paper to this conference, by this time I will submit to this journal - because they have to. They are always under pressure because their scholarship runs only for 3 years – 3.5years max. So the whole thing is driven by a time line rather than what you actually accomplish, and that’s very sad. When I was doing my PhD in the US, time was virtually unlimited and you got your PhD only when your professor thought you had done enough work and you could defend your thesis properly. That made a big difference, I think.

     

    H: And you think that has changed dramatically, since?

    S: Yes, at least in our education system in Australia. It is like a factory churning out PhDs, otherwise the university does not get its funding from the govt. The university gets a sum of money – quite a large sum of money, $ 80,000, roughly – from the government, for every PhD student it produces. So it is in the university’s best interest to churn out PhDs at the stipulated rate. The whole thing has become a bit distorted. I’m just hoping this will go in cycles and people will ultimately realise that this is not the way science should be done. And this business of having to find an immediate application for your science is another problem that is increasing. Some of the best science has been curiosity-driven, not through a desire to find a use for it. Einstein is a good example: he was working as a patent clerk and doing science as a hobby on the side. His scientific reserch had very little to do with the patents he was examining, and I don’t think it was inspired by them! Maybe that’s the best way to do science! I know I am sounding very idealistic

    Another problem is this constant pressure to get funding. You are seen as successful only if you have a large amount of funding and a huge number of people working in the lab, but that doesn’t necessarily lead to good science. I found that when I was younger, working with a smaller team of just 2-3 people, we were much more productive. We didn’t need a lot of money, we just needed to be left alone. We got a guaranteed small sum of money, we didn’t spend all our time writing grant proposals and we were left alone to do what we wanted. It worked beautifully and our productivity was so much better then compared to now. Now, I have a lot more money and a lot more people in my lab, but I don’t think we are doing great productivity-wise. It is somewhat dissatisfying.

     

    H: You mention applications are not the only motivation for your work. I take that to mean that it is a motivation, at least partially?

    S: No, not really. Our first interest, always, is to find out what makes these tiny creatures tick and tick so well. Curiosity-driven science is the main thing. If something useful comes out of it that’s well and good. We will see if we can incorporate that into a robot. Again we don’t try to be slavishly biomimetic. We don’t copy every detail of the insect, we don’t build a compound eye, we don’t have it flapping wings and so on. We just take some of the algorithms that we think we understand, e.g., the way the insect analyses the visual information and processes it to drive the behaviour, and use that algorithm as a starting point for designing an aircraft vision system. So, it’s really bioprincipic rather than biomimetic, because animals could have a particular design for several reasons and so copying them slavishly may not be very useful.

     

     H: Has this engineering application aspect been part of the research right from the beginning?

    S: No, not really. It came much later in life and it was really suggested by funding organisations. We found that . We just published this finding and left it alone, but then people started to use that idea to design navigation systems for robots going along corridors of buildings. It didn’t even occur to us. Someone else picked it up. Eventually, one of the big defence research funding organisations in the US called DARPA found out about our work and asked us if we would like to be involved in a project to apply some of our findings to design helicopter guidance systems.

     

     H: Are you ever worried about what kinds of uses the findings may be put to?

    S: It does worry me, but surprisingly, these defence organisations, e.g. the US air force, army and navy - we have gotten funding from all of them - seem very interested in the basic science, for some reason, even more I should say than some of the basic research funding organisations. They seem quite happy for us to publish our work and don’t put any embargo on it. It’s possible that our work was not sufficiently interesting to them! But yes, it does worry me from time-to-time, that I’m designing something that could be used for not very nice purposes, but so far I don’t think that’s happened. Also, once it is published, it becomes public domain knowledge, and we lose all control over how the findings may be used.

     

    H: I was at the European Society for Evolutionary Biology (ESEB) conference recently, where Laurent Keller, at the end of his ESEB presidential address, climbed up on the table and exhorted young biologists to not ignore unexpected results, or discard them as outliers or errors. Has serendipity or accidental discovery played an important part in your research too?

    S: A lot of the time. Going back to the , that was complete serendipity. We were just training bees to come into the lab through this hole and we just accidentally observed, we looked at them coming in, we noticed them coming in right down the middle and said, you know, how is this happening? So it was purely by serendipity. Other things, for example, . That again was done through just watching these bees when they come and land, and noticing that they came in rather rapidly at first and progressively slowed down as they approached the surface. We said let’s look at how they do this and simply filmed them in 3d as they were landing. Based on the properties of their trajectories we could tell that they were using a very simple method for landing - as the bee approaches the ground it always look at how rapidly the image of the ground is moving in its eye and adjusts its forward speed to fly slower and slower as it gets closer and closer. It occurred to us later that it is a very beautiful autopilot for landing - you don’t need to know how far away you are from the ground, you also don’t need to know how rapidly you are approaching the ground, and all you have to do is keep the image speed of the ground constant to make a beautiful smooth landing. t. So that’s again purely accidental. Just observations. And most of these things are not really what we said we would do when we put in in our grant application! That’s the thing you see - the grant - if you get it - keeps your lab going, but the things that make the big science are not often the things you said you would do.

    It comes down to this whole rather archaic idea that all science be hypothesis-driven, that need not always be the case, many of these things are chance observations right? You just observe something, you notice something, and then you form a hypothesis. It’s very difficult quite often to artificially manufacture a hypothesis just because the grant reviewer wants to see one. And the students are also taught that way, that the basic way to do science is to have a hypothesis first and then look at the various possibilities of how you test that hypothesis. I don’t think most science works that way at all. It’s just some illusion we have but we don’t want to admit it. I think it is very important to be able to play around with things without an exact hypothesis to start with. Hypothesis-driven science is useful, but it can’t be just that.

    Part 2 of interview :

     

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