An address to PhD students from NIMR and UCL at Mill Hill (London, UK) 16 May 2013. There is pdf version of this post here.
“It is difficult and often impossible to judge the value of a problem correctly in advance; for the final award depends upon the gain which science obtains from the problem. Nevertheless we can ask whether there are general criteria which mark a good mathematical problem……. A mathematical problem should be difficult in order to entice us, yet not completely inaccessible, lest it mock at our efforts. It should be to us a guide post on the mazy paths to hidden truths, and ultimately a reminder of our pleasure in the successful solution”
(D. Hilbert; Mathematical Problems. Address delivered to II International congress of mathematicians; Paris 1900).
In 1684 Edmund Halley went to Cambridge to try to get Isaac Newton interested in a dispute he had been having with Christopher Wren and Robert Hooke on whether the elliptical orbits of the planets could be explained by a force inversely proportional to the square of the distance from a center. Newton claimed to have solved the problem but could not find the papers so he sent him back to London and promised to do again the calculations. This got Newton going and within 16 months he produced his Principia in which he went beyond solving the ‘small’ problem of the elliptical orbits. Curiously I am told that, as it happens, the Principia do not contain the proof that Halley had asked for. Newton was just pouring into paper what he had been thinking and worrying about and sharing it with the world. And, of course, almost two hundred years later we have a similar episode when Charles Darwin receives a letter from some Alfred R Wallace from Indonesia with an explanation for the origin of species which kicks him into action to deliver his own, very similar but longer developed solution, of the same problem.
What these two well known stories have in common is that the people involved, all household names, were doing what they were doing for sport, for fun. Surely they cared about priority of discovery and competition (witness the bitter arguments between Newton and Leibnitz on Calculus or the gentle manoeuvring of Darwin’s friends with Wallace), but the thrust behind their work was that they loved it, they were driven by a natural inner curiosity and pursued Knowledge. They were not motivated by impact factors, careers or the Warholian fifteen minutes of fame afforded by a high impact publication. They genuinely valued and wanted to find out the workings of Nature and then, when they were ready, tell the world i.e. to publish (for an interesting perspective on Science, have a look at the collection of vignettes from Feynman’s “the pleasure of finding things out” BBC http://bbc.in/12m5F2T and for the whole thing: http://bit.ly/dJ0tia). It is not an accident that the questions these people asked were difficult, things that when known would and did, transform the world. But things have changed and in particular the last twenty years have seen a dramatic transformation of the fabric and the outer look of science, particularly the biomedical sciences. The pursue of knowledge has given way to the pursue of the publication and the significance of the finding is blurred by the impact of the journal in which the work is published. We have lost some perspective about what it is that we do, and most of the time we do not know why we do Science; also nobody asks us. This in part is the fault of my generation. The situation has changed too quickly and by the time we feel the consequences we find ourselves trapped in a very tangled web. The good news is that there is YOU and that that the future belongs to YOU –there is no more powerful weapon than having the future in ones hands- and this is why people like me have faith in you, not only to deliver the answer to many of the questions that some of us know lurk in the background of our falsely perceived knowledge of Nature, but also to create a different and better structure for the way we go about this quest. We also have a duty to guide you through the path to the solution ensuring that you do not make the mistakes that we have made. I shall come back to this but for now, allow me to thank you for the invitation.
It is a privilege to be here and to have the opportunity to share the day with you. There are few things more exciting for someone like me than to spend time with the likes of you, listening to your talks, to your interests and insights. So, THANK YOU. Natalie asked me to talk about my career path, particularly the choices I have made to get to wherever it is that I am. I shall be happy to tell you some of these. However, I want to tell you that they are not helpful to you. It would be foolish for me to suggest (as I have seen some of my colleagues do) that what I or they did, will work for you. The stage on which you operate is different. The world I made most of my decisions that took me here does not exist and was very far removed from the world of YouTube, Twitter, Impact Factors and hot publications…….as you will see. However, there might be something to learn from a reflection of those choices in today’s world. After all, we do have one thing in common: the excitement of finding out things about Nature and it is for this reason that I shall focus the choices on this common bond between us, the passion for Science. In the end, though, a most important thing today is to hear YOU and I look forward to questions you may have which might make this more interesting.
The first message I want to give you is that Science is something you have to love, something that either you have within you or you don’t. You can learn science but a scientist is something that either you are or you aren’t. Most people doing Science are not scientists, even if they are successful. Do not be surprised; if you think about it you will see that it is true. But let me step back. Taking this premise on board we can move on.
I come from Spain and grew up in a country and at a time where and when education was not valued. We were taught to read and write, had to memorize a lot of facts but, beyond this, you had to fend for yourself. There were no expectations about doing a PhD (what?), there were no goals other than the need to find a job and lead a good family life-and believe me, these are important values. This circumstance has good and bad elements associated with it. On the one hand it leads you to think on your own, to have an open mind and therefore to define your own questions, to shape your own view of the world. On the other hand there is no training, no predefined challenges nor a necessary intellectual discipline early on, like most of you have got. And this has its consequences: gaps which I have been trying to fill ever since. Somehow I decided to study Biology and from the beginning was captivated by Biochemistry, Genetics, the problems associated with the emergence of Life and, in particular, what we call Developmental Biology which in those days was Embryology. At some point two books felt into my hands: Jacques Monod’s “Chance and Necessity” and Conrad H. Waddington’s (yes of the Waddington landscape) compendium “Towards a theoretical biology”. Both stimulated me in convergent ways. Monod’s book made me think very seriously about biological systems as chemical machines. It is interesting that Monod promises in the book a treaty on molecular cybernetics which, unfortunately he never delivered. “Towards a theoretical biology” led me to consider something which, in those days, was not possible –though I did not know. “Towards a theoretical biology” is a summary of a series of conferences organized by Waddington on the thought of the title: the possibility of a theoretical framework for Biology, which took hold of my ignorance. Bored by Botany and Zoology (the way they were taught in Spain) I had become interested in physical and organic Chemistry and was very impacted by the beauty of the logic and organization of Chemistry. If Chemistry was Physics and Biochemistry underpinned Genetics and Cell Biology, could one not work out Biology from Chemistry?……..perhaps….one could find some Physical principles in Biology…… I decided to try to learn some physics and some maths…..but it was too late…..and for theory in Biology, it was too early. Still, these readings sew a seed that has been with me all my life.
At the end of my undergraduate and military duties, I got a chance to do a PhD in the US and went to The University of Chicago (USA), a place with a history on Theory in Biology. Inadvertently this was a good choice and the reason is the one thing I learnt then which I share with you: in our trade, the choice of where to work is very important. Not the person to work with/for/under/over, but the place, and it is a good thing to choose one (if you can, and I think you all can) that has a lot going on because if something goes wrong in your first choice, you have a lot to choose from around. This was important to me because ….things did go wrong in Chicago. What I wanted to do was to develop a Theoretical Biology with a strong basis in Physical Chemistry but….in Spain nobody had told me that we did not know enough Biology for this and that for Theory to emerge you need facts, experimental results, not only ideas…….in some ways Science, Biology in particular, is the story of beautiful theories turned into ashes by ugly facts. And it was the dearth of and scorn for facts that is at the heart of the failure of that Theoretical Biology. Nonetheless three good notions came up from the Waddington exercise: Positional Information, Waddington’s epigenetic landscape and the clock and wavefront model for somitogenesis. All grew out of the need to frame experiments and the first two of these have been important in my life but in the 70s there were just ideas. So, admitting that I had made a mistake, I opened my eyes and my ears, and learnt that indeed, we did not know much about the building blocks of development……we did know about metabolism, and I have to admit that, as I have said, I did love the intersection of Chemistry and Life…..but as we know today, development is not JUST about metabolism. In the late 70s all was up for grabs, the molecular underpinning of developmental processes beckoned. And thus, two years into my PhD I realized that I had made a mistake and began to do ‘proper Biology’, experiments. Nonetheless my toilings those two years had not been in vain. I had learnt about Turing, very importantly about Statistical Mechanics but realized that in order to apply all this to development, one needed to learn about the fabric of Developmental systems and this was on the way. I began to appreciate Genetics, did a PhD in molecular genetics and in the course of this work I saw Ed Lewis’s paper on bithorax and what is now known as the “Nüsslein Volhard screen”. Both were interesting, more than that and as I was beginning to think about Genetics, both challenged me and pointed out concepts that have been developed over the years since: programmes, tools, structure in systems.
So, I forgot about Physics and Biology and after completing a PhD on something which I was not too interested in, but which taught me a lot about Biology (at the height of molecular genetics), I came to the UK and spent the next twenty years chasing genes and their interactions in Drosophila. Probing how their functions map to different aspects of development and struggling to understand how and what it is that they control. I have not been a main player in all this but have been fortunate, very fortunate, to do this work at a time where lots was happening, when every month we learnt something knew about what drove a particular process. I also have been lucky to work with talented and inspiring people, people like Phil Ingham, Michael Akam, Peter Lawrence and in particular Michael Bate. But also Postdocs and students, many of who have taught me a great deal. And here a piece of advice, you need to talk to interesting people. Your supervisor is, sometimes, important but need not be the center of your intellectual life. Both as a student and a postdoc I always found mentors, gurus, interesting people who were always happy to have a cup of coffee or a chat and who opened my mind to much that was and is both important and interesting. It’s one of the privileges of our job that many people do not exploit: the freedom to interact with people and to learn from them.
The 80s and the 90s was the time in which mutants turned into genes and genes into patterns of expression and it was left to us, in an exercise which I have sometimes called ‘palm reading’ to use Genetics to get back from here to function, to integrated function. Those years were a very good time to work in Drosophila because it was the best organism to learn about development and I did it in a place, the LMB, where the C. elegans tradition had laid out the same basis about development and how to do this. The fact that Drosophila and C. elegans developed in parallel was important for me to behold and learn from. Genetics lifted the veil of mystery surrounding the connection between genes and development. My main interest throughout this time was the integration of information and this led me to work on the interactions between Notch and Wnt signalling which have taken and will take a lot of my time and attention. But this is a different story which you can follow in my publications, if you so choose.
By the end of the 90s we, as a community, had a pretty good idea of the make up of living systems and of the molecular devices which drive development. The genetics of model organisms had yielded a remarkable picture of conserved transcription factors and signalling molecules, with some exciting puzzles like the Homeobox (which still remains a puzzle). The zebra fish and the mouse were following in the footsteps of these organisms and were beginning to open up their secrets. A universality of plan at the genetic level was emerging. In many ways, by the end of this time, one could agree with Stephen J. Gould that ‘for sheer excitement, Evolution as an empirical reality, beats any myth of human origins by light years. A genealogical nexus stretching back nearly a billion years and now ranging from bacteria…to the highest Redwood tree, to human footprints in the moon. Can any tale of Zeus or Wotan top this? When truth value and visceral thrill thus combine then, indeed, as Darwin stated in closing his great book, there is grandeur in this view of life” (SJ Gould, Science 1999; 284, 2087 Darwin’s more stately mansion).
But, what did we know about the function of all these genes? How did they make a cell, let alone an organism? How did it all work together? We did know the alphabet, but did we (do we) know the syntax? We have the parts, but how do they come together into a functional whole? Genetics has been an amazing tool of discovery but, alone and in the manner that we have used it so far, it might not be the tool of choice to see how a cell actually works not even how it is functionally organized (two comments on this: http://bit.ly/10fZkmK and http://bit.ly/185sZp5). It seems to me that we have not risen to the challenge and that for the last ten years we have been bootstrapping a collection of parts that has a collectionist, rather than an engineer, flavour to it. How can we progress? Biological systems not only produce the attractive patterns that seduce us, they also produce numbers and rhythms: think of the way homeostasis of a tissue like the skin or the blood works, think of how your two arms (which have never been in touch) grow to pretty much the same distance and with the same proportions, think of the time course of events which are the same in you and in me. Can genes produce these numbers? Sure they are ‘encoded’ in the genes but, how are they decoded?
While learning genetics with Drosophila, I had been following pieces of work that tackle the behaviour of single cells and at this I would like to mention the work of Tariq Enver who probably was the first person to realize that the behaviour of single cells could be different to that of their ensembles. The reason why this was important lay in the principles of statistical mechanics which saw the properties of an ensemble as a result of the statistical averaging of large populations of its components. Around the year 2000 I had the good fortune of attending a small conference at Les Treilles in Provence, where I heard two talks that had a big impact on me. One was by Michael Elowitz, the other one by James Ferrell. I was “bowled over”. Elowitz’s talk was about noise in gene expression in bacterial systems, Ferrell’s on the behaviour of signalling systems at the level of single cells. Both contained a mixture of theory and experiment that I had yearned for. Both emphasized the importance of measurements and of how to use measurements, detailed measurements, to guide our thinking. At the same meeting, Ernst Stelzer (of confocal microscopy fame) made a statement which has followed me since: biologists, he said, do not know how to make a measurement and this is most obvious in their (our) failure to distinguish between an average and a distribution. It is true and, understanding this will change your view of biology. We have made a science of averages while the information lies in the distributions. All together, the three days at Les Treilles changed my mind, again, and reminded me of my interest to piece together life, development from its components. A statistical mechanical approach to Biology was not possible in the late 70s, but perhaps now, it was. I decided to try to think along the lines of Elowitz, Ferrell and others, in particular Leibler and Alon, and see if this had something to do with development. But, was Drosophila the system to pursue this? The answer was no.
I wanted a system in which one could collect data at the level of single cells, where we could record events over time and which, if possible, could have genetics. Furthermore, if it was simple, this would be great. Embryonic Stem (ES) cells have provided me with such a system and over the last few years, together with a very talented group of people, we have been probing what I would like to call the “inner structure of biological systems”. It is early days, but I believe that they, ES cells, are a good system to gain insights into this as a guide to the inner structure of biological systems. They allow measurements of just about anything you want to measure at the level of single cells, they allow averaging and dynamic analysis, they make choices that follow those that cells make in embryos and they represent the challenge of using them to reconstruct organs and embryos. They offer the possibility of realizing a statistical mechanics of biological systems; from component elements (molecular devices) to macroscopic variables (phenotype).
However, where we seach for those laws, principles, whatever, is not relevant. Each of us might have our favourite system. What we need to do is to acknowledge that the aim at the moment is not ONLY to gather more components, but to put them together and to look for quantitative targets. We need to change our mindset because we want to follow Richard Feynman and build systems in order to show that we understand them. To do this we need to penetrate their inner functional structure which is not just a collection of pieces. To see what is happening I would like to remind you of the story of Treasure Island. As it turns out, Robert L. Stevenson wrote Treasure Island around a map, which his nephew and he had been drawing. When the book was finished, he sent it to London for printing but he sent the map separately. The book made it, the map did not. He wanted the map and not having a copy, he had to infer it from the narrative. This was frustrating as he knew that whatever he did, the original map never produced itself. This is exactly the situation that we faced in Biology, particularly Developmental Biology. We have an advantage over Stevenson, though we do not have the map, we have its outcome: the cell, the organism. And we can see that the map that the narrative of Genetics produces, never matches the blueprint that produces a neuron or a rose (for an extended version of this idea, see “Maps: resolution and insight in Biology http://bit.ly/11JnvBF).
I cannot end up without addressing the current structure of Science, in particular of the Life sciences. The reason to do this is because it affects you and because, as I said at the beginning, you have the opportunity –if not the power- to change it. It is a measure of where we are that today in order to do Research, it is not enough to have good questions or interesting answers, that you, me, us, need to consider the framework within which we work, that we need to ‘sell our projects’ to ‘pitch them’ and therefore we need to be part salespeople. Sure this has happened before, but then there was room for the scientist who lacked those skills. Not today. Research has become expensive, the funds are not easy to get and basic research is difficult to justify. Furthermore, we have conflated content with impact and fashion, have confused intellectual potential with the glitter of certain publications on which we rely to gauge the ‘short term’ value of our work. This has consequences and I am afraid that half or more of you might not survive in this environment so: be careful. Change will come but will come slowly. The pace will depend very much on you and whether you choose to stick to the methods that we have created for you or to move forward and live with the times. The problem, the main problem, is that we are working within a structure from another time, catering for other needs, which has grown without adapting and now is making water. The methods of funding, of selection for jobs, above all the procedures of presenting and publishing our results belong to the 60s and the 70s but the materials we work on and the environment is not the same. Surely we need to adapt too (see the interesting posting http://bit.ly/U423za from Casey Bergman on scientific growth in the XX century) but we are not doing it. Music, literature, journalism have been changed by the web but we only use the web to make our work more cumbersome. We need imagination, we need you to take what is good from us and turn it into something that works for everybody. I have seen very bright people, real scentists, quit and I do not like this.
Notice that the system that we have is one that has worked for….. those who created it and run it …but it is making water and we need to change it. Open Access is a good thing but, Peer Review, the evaluation of impact, the organization or research teams, the connection between basic and applied research, the relationship between Universities and Research Institutes, these are THE issues that need addressing. We will address them…however, while we get there, you can contribute with your choices, with your attitudes. Remember, or let me tell you, that you are the privileged ones and that with privilege comes responsibility. Many of you will lead the future and I would encourage you to lead change because though Science has an important individual component, it is today more than ever, a team work.
Never compromise your principles and interests for short term gains. Remember that the real prize does not lie in the accolades that you receive but in the joy, the wonder of seeing something for the first time and even better, to know, that it might be important. As the pianist Glenn Gould said about Art, I say about Science, it should not be “the release of a momentary ejection of adrenaline but the lifelong construction of a state of wonder and serenity”.
Some people like to look back with nostalgia and think that their time, that in which they were your age was very good, the best. There might be some truth in this in so far as those times the community was small, our ignorance large and the questions few and well defined. But I would say the situation now is better; we know more and we can know more. There was a golden age for uncovering the pieces, there is now the golden age to put them together. Remember because we know the components we do not know how they work together. I shall not abound on metaphores about this. Instead, let me tell you a few problems (in the spirit of Hilbert in the opening quotation) of problems that are both important and interesting, in developmental biology. Furthermore, they are open. Here you have them:
- What is the scale of biological processes? how many molecules are involved in specific processes? What are the time scales of molecular and cellular events? We need to measure.
- There is an intuition that biological systems are hierarchically organized but we know little about this structure. What are the networks, the functional networks of the cell? How are they linked at different levels (molecular to cellular)?
- How do cells generate time? We do know a bit about this from the circadian clocks but there are other clocks associated with homeostasis and dynamics associated with development.
- What is the role that mechanotransduction plays in development? How do cells sense and react to density?
- What is the relationship between the programme and the organism.
Key in the work towards the answer to these problems is the need to measure, to be precise in the design and execution of the experiment, to have quantitative predictions. Biology needs to change and become more quantitative.
I shall finish where I started. You have the most powerful weapon that you can have: the future in your hands, the future in your future. You live at a time when you are empowered by technology to find, just about anything you want to find out, and by the internet to develop new, efficient, useful and fair ways of disseminating your findings. Be creative ad brave. And to this add that a most important thing in Science is to have a good question. Today, though, you need to have a pragmatic approach, you need to do something that will allow you to survive and which does not distance you from your interest, but do not forget that interest, that passion. One of my colleagues said once: I do not have interests, I have passions. He was/is a scientist. Never forget that the real reward, the real prize is not a paper in Cell, Nature or Science, but the actual thrill of finding something new and interesting, to peer through an experiment and see, for the first time, something about Nature that was hidden before you saw it. If you are a scientist, you will recognize that moment. Do not let anything destroy it. Treasure it. It is the only thing that nobody will take away from you. When things get tough, and they will, get back to it to remember what all is about. Ah, and help us change this so that, though in a different manner, Science can regain its rightful value and place.