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 :