Increasingly, the biological sciences bask in short lived small bites of ‘success’ where the publication rather than its content and real impact (as opposed to that of the journals) rules. Highthroughputness, terabytes of information, large genome data analysis, saturation screens, all form part of a culture with little time for pause, reflection and ponder. Perhaps it is because of the prevalence of these attitudes that meetings to celebrate the contributions of senior scientists provide an opportunity to appreciate what it is that we are missing in the current structure of the biological sciences.
On December 14 (2013) a symposium took place in Cambridge on the “specification and development of neural circuitry’ to celebrate the 70th birthday and science of Michael Bate. The meeting, organized by Alicia Hidalgo and Matthias Landgraf, brought together a group of old and young developmental neurobiologists around individuals who had been associated with Mike throughout his career. For those outside the field of Developmental Neurobiology –but not if you live in Europe- it is easy to overlook Mike. His quiet, science centered attitude, far from the limelight, looking at Nature in the face and finding out how it works, contribute to this. But the impact of his work is anything but quiet. His legendary teaching, in particular in Cambridge, Cold Spring Harbor and Bangalore, as well as the many graduate students, postdocs and PIs he has inspired, place him amidst a small group of people with real impact in modern Biology and whose work should be an example to us.
His toilings span over 50 years in a trajectory that when woven together, reveals a unity of direction and content. Much of Biology is about form and function and Mike’s career represents a modern approach to this problem. His lifelong interest has been to understand how neural circuits are put together and whether their development reveals a logic to their function i.e. whether understanding how form arises might not contain insights and reasons about function. To do this he developed over time a rare blend of neuro- and developmental biology. One can see this emerging, in a rather prescient and programmatic manner, in the publications of his PhD thesis, done under the supervision of John Treherne in the Department of Zoology in Cambridge, on the gin trap of a moth and published in the three papers in the Journal of Experimental Biology in 1973. In the introduction to the first paper he lays down his research agenda: “the aim of the present paper is to define a simple case of neuronal differentiation where the techniques already used in the investigation of pattern formation in the insect epidermis might be applied to the mechanisms which regulate the central connections of the epidermal sensilla” (Bate, M. J.Exp. Biol. 1973 59, 109-119). The work is an interesting combination of physiology, theory and some developmental biology, pretty much the combination that would run through his scientific life. Behind the attention to the detail there has always been a big theme laid out by the work of the late D M Wilson who, as Mike pointed out many times, poses questions about our notions of biological design upon pointing out that the flying circuits for the locust are in place before the locust needs to fly (implicitly, before they could have been selected for the function they are being built).
After his PhD, Mike undertook a life of moving around with important stops in Canberra (Australia) and Tubingen (Germany), a time during which he matured his thoughts on how to tackle the problem of the emergence and assembly of neural circuits. In 1976 he produced two seminal pieces of work, one on pioneer neurons (Bate, M. 1976 Nature 260, 54-56) and the other, “Embryogenesis of an insect nervous system. I. A map of the thoracic and abdominal neuoblasts in Locusta migratoria” (Bate, M. 1976 JEEM 35, 107-123). Two years later, he produced a second important paper on the ground plan of the insect nervous system: , “Embryogenesis of an insect nervous system. II. A second class of neuron precursor cells and the origin of intersegmental connectives” (with Grunewald, 1978 JEEM 61, 317-330). These three papers were seminal because of what they established, launched and inspired. A nervous system, at least in the first instance the insect nervous system, was revealed to be built stepwise, making use of cell driven precise and identifiable processes. During the laying down of its ground plan, the central nervous system used identifiable cells that performed defined tasks of pioneering an otherwise blank slate of the tissues through which the axons and the system had to navigate. Cells born afterwards would track those paths and the development of the system could thus be linked to its developmental engineering. The papers were much ahead of their time and conceptually laid the foundations for a long and interesting research agenda. The notion of working with single identified cells to study their behaviour and contributions during development was born and later on when genetics broke the black box that was its molecular underpinning, this work was the foundational reference.
Mike had worked with locust because, as he pointed out many times, the embryos were big and the cells large. This was important as the purpose of the exercise then was to identify the tracks as they were laid down and how these related to cells. So, size mattered for the eyes and for the tools: scalpels, needles, stains and microscopes and, of course, no antibodies, no Gal4 lines that would identify single cells. The consequences of this work were huge and only time puts them in the correct perspective. At this time he entered into an immensely fruitful collaboration with Corey Goodman, one of the people he inspired and led. One important challenge in this collaboration was, as Goodman recalled at the meeting, to get to see the blueprint of the Drosophila nervous system in the embryo. The reason for this was not only one of completeness –observation of the blueprint in
all insects- but the need to hack into Drosophila to take advantage of the powerful genetic tools that were emerging at the time. The difference in size between the two is large –Drosophila is about 20 times smaller than the locust and dealing with this, in pre-antibody
days, required skill and insight. Mike managed to reveal this structure through a combination of his unique skills in dissection and observation and thus led the way to show a conserved body plan for the groundplan of the arthropod nervous system laid out in a landmark paper (“From grasshopper to Drosophila: a common plan for neuronal development” Thomas, JB, Bastiani, M., Bate, M and Goodman, C. 1984 Nature 310, 203 – 207). The path was now laid to use Drosophila to get the molecules and the Goodman lab, as Goodman himself recalled at the meeting, went on overdrive to identify genes and proteins involved in the pathfinding: a stunning collection of genes and mechanisms that were uncovered over the next few years. It could be argued that the genetics of Drosophila would have revealed all this. Maybe. Or most likely not, because while it might have thrown out genes and painted paths, only the slow, thoughtful, careful work that preceded these experiments, created the questions (and they were the right ones) that needed to be addressed by the genetics. A consideration of the watershed work of Goodman’s laboratory highlights that the difficult thing is to know what one wants to know, to map out the right terrain, before one launches into finding out the machine that runs the process. If we do not understand flying we cannot understand the machines that do the flying.
Mike was not directly involved with the opening of the genetic Pandora’s box of axonal pathfinding but without his contribution the content of the box would have been, for a while, just a collection of genes. At this time, in characteristic fashion he went to explore another virgin territory: the muscles. This time directly to Drosophila. Once more with a combination of his best tools – insight, dissections, needles, stains – and looking at what the cells did without the bias of the genetic or molecular analysis, he now uncovered the groundplan of the muscle system in Drosophila (Bate, M. The embryonic development of the larval muscles of Drosophila. 1990 Development 110, 791-804). Once again he opened up a new field of study and, guided by what the embryo told him, he laid down the questions that would be pursued in the future. He uncovered a blueprint based on muscle founder cells which resembled, in many of their abstract properties, the neuroblasts he had mapped earlier, and saw how this plan developed into a pattern where the properties were not just tracks of axons, as in the nervous systems, but the sizes and orientation of the muscles. And in this work, we can see again, the leitmotif of the need to understand development to link form and function: “It may well be that the assignment of these properties to the muscle precursors, like the specification of neuroblasts, depends on prior regionalization……..to understand this process in detail we have now to combine the description given here with a genetic analysis of muscle development”. And this time, he did pursue this himself led by two postdocs Mary Baylies and Mar Ruiz Gomez. But there was more to this work. This was not some explorer going into unknown territory to add to some geography of the insect embryo. What Mike wanted, wants, to understand is the emergence of circuits and their inner functional logic, and the neuromuscular junction provided a basis to think about this. Perhaps there was some functional reason why there are 30 odd neuroblasts and 30 odd muscle precursors. In parallel with the genetic analysis of the muscle system, together with a student Kendal Broadie, in the 90s he began to chart emergence of neural activity during development. Slowly this finally evolved to the emergence of circuits and in a long standing collaboration with Matthias Landgraff, the functional mapping of the development and function of the myotopic map of the Drosophila larva. When looking at his most recent work with the perspective of time it is difficult not to think of the lines from TS Eliot: “and the end of all our exploring will be to arrive where we started and know the place for the first time.”
Perhaps the myotopic map was the goal when looking at the gin trap in the moth. Sometimes our research moves through curious paths and, if one is lucky, one can see that one is close to the place one wanted to be. That this might apply to Mike was much in evidence at the Symposium, where we also had a chance to see the effect that he and his work have had on people. One aspect that became clear in many talks, but particularly in C. Goodman’s. C. Doe’s and J. Truman’s, was how Mike’s career has always been about seeing things and laying down the ground for others before anybody was there or thought of doing that. Like the true enlightening pioneers, only when he revealed something, it was clear to everybody else that it was what they should be looking at. His work also illustrates that, to do this one needs to have the time and the space to look, see and think. One recurrent theme at the meeting was the role that Janelia Farm plays in modern neurobiology. Here, again, one could not help seeing the influence of Mike, as many of the leading people working there are connected to him and the questions on circuitry so elegantly tackled there are related to his work and interests. The question, of course, is whether much of what is true of Drosophila and other insects will be true of vertebrates. Marco Tripodi touched upon this at the meeting. Time will tell. There is much to be learnt but what there is little doubt about is that the methods and intellectual framework laid down by Drosophila will be important in the understanding of vertebrates. The Symposium was closed by Vijay Raghavan, a close friend and collaborator who extolled the contributions of Mike to the development of Drosophila genetics and cell biology in India.
I had the privilege of sharing much time and space with Mike for 13 years in the basement of the Department of Zoology at the University of Cambridge. This was a most important time for me as through our interactions and seeing him at work, it taught me how to ask questions and think about Biology. In all this, amidst much that the passing of time highlights as important there are two specific things that I learnt from Mike, that I cherish and that I try to pass on to the new generations of scientists. The first one is that the pursuit of Science is not about personal visibility, but about developing an ability to see into the system one is studying. That the prize of research does not lie in being seen, but in seeing. That a publication is simply a report of the observations, work in progress, and, more important, part of a thinking process, rather than the goal and a passport for a short lived glory. The impact that he has had on the field and on people has come from what he has done and revealed and not by where he has published. We should all take stock of this. The second thing I learnt is very important and should be at the basis of cell and developmental biology: how to observe. When going to the microscope –or looking at any experiment- one should be prepared to let the system talk. One should listen with ones eyes to what the preparation says and not override this with what one wants to see. There is always more in there than we can see and only letting ourselves be drawn into it, we shall be able to see it. This attitude is the prevalent one in his 1976 and 1990 papers on neuroblasts and muscles and says how much one can learn from this approach. But in the end, like many others, it was listening to him teach and talk that reminded me always, what science should be about. There is little doubt that Mike has created a school, a school of thinking and of watching, and much of this without really planning to do so, simply because of his way to do Science, something that many of us would like to see returned. With the possibilities of today, blended with thought and insight, the results could be enormous.
What emerged from the excellent meeting in Cambridge was a pulsating story of science, developed over time by people working constructively on each other’s ideas through carefully crafted experiments addressing well thought-out questions. Low throughput biology with high content and an impact clearly defined by the careers and research that it has launched.
Happy birthday Mike and, together with many others: thank you.