著名数学家研究经验集

� 1000 VIII. Final Perspectives Borwein, J., D. H. Bailey, and R. Girgensohn. 2004. Exper- imentation in Mathematics: Computational Paths to Dis- covery. Wellesley, MA: A. K. Peters. Calkin, N., and H. S. Wilf. 2000. Recounting the rationals. American Mathematical Monthly 107:360–63. Ferguson, H. R. P., and R. W. Forcade. 1979. Generaliza- tion of the Euclidean algorithm for real numbers to all dimensions higher than two. Bulletin of the American Mathematical Society 1:912–14. Gessel, I. 1990. Symmetric functions and P -recursiveness. Journal of Combinatorial Theory A53:257–85. Graham, R. L., D. E. Knuth, and O. Patashnik. 1989. Concrete Mathematics. Reading, MA: Addison-Wesley. Greene, C., and Wilf, H. S. 2007. Closed form summa- tion of C-finite sequences. Transactions of the American Mathematical Society 359:1161–89. Lenstra, A. K., H. W. Lenstra Jr., and L. Lovász. 1982. Factor- ing polynomials with rational coefficients. Mathematische Annalen 261(4):515–34. McKay, B. D., F. E. Oggier, G. F. Royle, N. J. A. Sloane, I. M. Wanless, and H. S. Wilf. 2004. Acyclic digraphs and eigen- values of (0,1)-matrices. Journal of Integer Sequences 7: 04.3.3. Mills, W. H., D. P. Robbins, and H. Rumsey Jr. 1987. Enu- meration of a symmetry class of plane partitions. Discrete Mathematics 67:43–55. Petkovšek, M., and H. S. Wilf. 1996. A high-tech proof of the Mills–Robbins–Rumsey determinant formula. Electronic Journal of Combinatorics 3:R19. Petkovšek, M., H. S. Wilf, and D. Zeilberger. 1996. A = B. Wellesley, MA: A. K. Peters. Wilf, H. S. 1992. Ascending subsequences and the shapes of Young tableaux. Journal of Combinatorial Theory A60: 155–57. . 1994. generatingfunctionology, 2nd edn. New York: Academic Press. (This can also be downloaded at no charge from the author’s Web site.) VIII.6 Advice to a Young Mathematician The most important thing that a young mathematician needs to learn is of course mathematics. However, it can also be very valuable to learn from the experiences of other mathematicians. The five contributors to this article were asked to draw on their experiences ofmath- ematical life and research, and to offer advice that they might have liked to receive when they were just setting out on their careers. (The title of this entry is a nod to Sir Peter Medawar’s well-known book, Advice to a Young Scientist.) The resulting contributions were every bit as interesting as we had expected; what was more surprising was that there was remarkably little overlap between the contributions. So here they are, five gems intended for youngmathematicians but surely destined to be read and enjoyed by mathematicians of all ages. I. Sir Michael Atiyah Warning What follows is very much a personal view based on my own experience and reflecting my personality, the type of mathematics that I work on, and my style of work. However, mathematicians vary widely in all these char- acteristics and you should follow your own instinct. Youmay learn from others but interpret what you learn in your own way. Originality comes by breaking away, in some respects, from the practice of the past. Motivation A research mathematician, like a creative artist, has to be passionately interested in the subject and fully dedicated to it. Without strong internal motivation you cannot succeed, but if you enjoy mathematics the sat- isfaction you can get from solving hard problems is immense. The first year or two of research is the most difficult. There is so much to learn. One struggles unsuccess- fully with small problems and one has serious doubts about one’s ability to prove anything interesting. I went through such a period in my second year of research, and Jean-Pierre Serre, perhaps the outstanding math- ematician of my generation, told me that he too had contemplated giving up at one stage. Only the mediocre are supremely confident of their ability. The better you are, the higher the standards you set yourself—you can see beyond your immedi- ate reach. Many would-bemathematicians also have talents and interests in other directions and they may have a dif- ficult choice to make between embarking on a mathe- matical career and pursuing something else. The great Gauss is reputed to havewavered betweenmathematics and philology, Pascal deserted mathematics at an early age for theology, while Descartes and Leibniz are also famous as philosophers. Some mathematicians move into physics (e.g., Freeman Dyson) while others (e.g., Harish Chandra, Raoul Bott) have moved the other way. You should not regard mathematics as a closed world, and the interaction between mathematics and other disciplines is healthy both for the individual and for society. � VIII.6. Advice to a Young Mathematician 1001 Psychology Because of the intense mental concentration required in mathematics, psychological pressures can be consid- erable, even when things are going well. Depending on your personality this may be a major or only a minor problem, but one can take steps to reduce the ten- sion. Interaction with fellow students—attending lec- tures, seminars, and conferences—both widens one’s horizons and provides important social support. Too much isolation and introspection can be dangerous, and time spent in apparently idle conversation is not really wasted. Collaboration, initially with fellow students or one’s supervisor, has many benefits, and long-term collabo- ration with coworkers can be extremely fruitful both in mathematical terms and at the personal level. There is always the need for hard quiet thought on one’s own, but this can be enhanced and balanced by discussion and exchange of ideas with friends. Problems versus Theory Mathematicians are sometimes categorized as either “problem solvers” or “theorists.” It is certainly true that there are extreme cases that highlight this divi- sion (Erdo˝s versus Grothendieck, for example) butmost mathematicians lie somewhere in between, with their work involving both the solution of problems and the development of some theory. In fact, a theory that does not lead to the solution of concrete and interesting problems is not worth having. Conversely, any really deep problem tends to stimulate the development of theory for its solution (Fermat’s last theorem being a classic example). What bearing does this have on a beginning student? Although one has to read books and papers and absorb general concepts and techniques (theory), realistically, a student has to focus on one or more specific prob- lems. This provides something to chew on and to test one’s mettle. A definite problem, which one struggles with and understands in detail, is also an invaluable benchmark against which to measure the utility and strength of available theories. Depending on how the research goes, the eventual Ph.D. thesis may strip away most of the theory and focus only on the essential problem, or else it may describe a wider scenario into which the problem nat- urally fits. The Role of Curiosity The driving force in research is curiosity. When is a par- ticular result true? Is that the best proof, or is there a more natural or elegant one? What is the most general context in which the result holds? If you keep asking yourself such questions when reading a paper or listening to a lecture, then sooner or later a glimmer of an answer will emerge—some pos- sible route to investigate. When this happens to me I always take time out to pursue the idea to see where it leads or whether it will stand up to scrutiny. Nine times out of ten it turns out to be a blind alley, but occasionally one strikes gold. The difficulty is in know- ing when an idea that is initially promising is in fact going nowhere. At this stage one has to cut one’s losses and return to the main road. Often the decision is not clear-cut, and in fact I frequently return to a previously discarded idea and give it another try. Ironically, good ideas can emerge unexpectedly from a bad lecture or seminar. I often find myself listen- ing to a lecture where the result is beautiful and the proof ugly and complicated. Instead of trying to fol- low a messy proof on the blackboard, I spend the rest of the hour thinking about producing a more ele- gant proof. Usually, but not always, without success, but even then my time is better spent, since I have thought hard about the problem in my own way. This is much better than passively following another person’s reasoning. Examples If you are, like me, someone who prefers large vistas and powerful theories (I was influenced but not con- verted by Grothendieck), then it is essential to be able to test general results by applying them to simple exam- ples. Over the years I have built up a large array of such examples, drawn from a variety of fields. These are examples where one can do concrete calculations, sometimes with elaborate formulas, that help to make the general theory understandable. They keep your feet on the ground. Interestingly enough, Grothendieck eschewed examples, but fortunately he was in close touch with Serre, who was able to rectify this omis- sion. There is no clear-cut distinction between exam- ple and theory. Many of my favorite examples come from my early training in classical projective geom- etry: the twisted cubic, the quadric surface, or the Klein representation of lines in 3-space. Nothing could be more concrete or classical and all can be looked at � 1002 VIII. Final Perspectives algebraically or geometrically, but each illustrates and is the first case in a large class of examples which then become a theory: the theory of rational curves, of homogeneous spaces, or of Grassmannians. Another aspect of examples is that they can lead off in different directions. One example can be generalized in several different ways or illustrate several different principles. For instance, the classical conic is a rational curve, a quadric, and a Grassmannian all in one. But most of all a good example is a thing of beauty. It shines and convinces. It gives insight and understand- ing. It provides the bedrock of belief. Proof We are all taught that “proof” is the central feature of mathematics, and Euclidean geometry with its care- ful array of axioms and propositions has provided the essential framework for modern thought since the Renaissance. Mathematicians pride themselves on absolute certainty, in comparison with the tentative steps of natural scientists, let alone the woolly thinking of other areas. It is true that, since Gödel, absolute certainty has been undermined, and the more mundane assault of computer proofs of interminable length has induced some humility. Despite all this, proof retains its car- dinal role in mathematics, and a serious gap in your argument will lead to your paper being rejected. However, it is a mistake to identify research in math- ematics with the process of producing proofs. In fact, one could say that all the really creative aspects of mathematical research precede the proof stage. To take the metaphor of the “stage” further, you have to start with the idea, develop the plot, write the dialogue, and provide the theatrical instructions. The actual produc- tion can be viewed as the “proof”: the implementation of an idea. In mathematics, ideas and concepts come first, then come questions and problems. At this stage the search for solutions begins, one looks for a method or strat- egy. Once you have convinced yourself that the prob- lem has been well-posed, and that you have the right tools for the job, you then begin to think hard about the technicalities of the proof. Before long you may realize, perhaps by finding counterexamples, that the problem was incorrectly for- mulated. Sometimes there is a gap between the ini- tial intuitive idea and its formalization. You left out some hidden assumption, you overlooked some techni- cal detail, you tried to be too general. You then have to go back and refine your formalization of the problem. It would be an unfair exaggeration to say that mathe- maticians rig their questions so that they can answer them, but there is undoubtedly a grain of truth in the statement. The art in good mathematics, and mathe- matics is an art, is to identify and tackle problems that are both interesting and solvable. Proof is the end product of a long interaction between creative imagination and critical reasoning. Without proof the program remains incomplete, but without the imaginative input it never gets started. One can see here an analogy with the work of the creative artist in other fields: writer, painter, composer, or architect. The vision comes first, it develops into an idea that gets tentatively sketched out, and finally comes the long technical process of erecting the work of art. But the technique and the vision have to remain in touch, each modifying the other according to its own rules. Strategy In the previous section I discussed the philosophy of proof and its role in the whole creative process. Now let me turn to themost down-to-earth question of inter- est to the young practitioner. What strategy should one adopt? How do you actually go about finding a proof? This question makes little sense in the abstract. As I explained in the previous section a good prob- lem always has antecedents: it arises from some back- ground, it has roots. You have to understand these roots in order to make progress. That is why it is always better to find your own problem, asking your own ques- tions, rather than getting it on a plate from your super- visor. If you know where a problem comes from, why the question has been asked, then you are halfway toward its solution. In fact, asking the right question is often as difficult as solving it. Finding the right context is an essential first step. So, in brief, you need to have a good knowledge of the history of the problem. You should know what sort of methods have worked with similar problems and what their limitations are. It is a good idea to start thinking hard about a prob- lem as soon as you have fully absorbed it. To get to grips with it, there is no substitute for a hands-on approach. You should investigate special cases and try to identify where the essential difficulty lies. The more you know about the background and previous meth- ods, the more techniques and tricks you can try. On � VIII.6. Advice to a Young Mathematician 1003 the other hand, ignorance is sometimes bliss. J. E. Lit- tlewood is reported to have set each of his research students to work on a disguised version of the Rie- mann hypothesis, letting them know what he had done only after sixmonths. He argued that the student would not have the confidence to attack such a famous prob- lem directly, but might make progress if not told of the fame of his opponent! The policy may not have led to a proof of the Riemann hypothesis, but it certainly led to resilient and battle-hardened students. My own approach has been to try to avoid the di- rect onslaught and look for indirect approaches. This involves connecting your problem with ideas and tech- niques from different fields that may shed unexpected light on it. If this strategy succeeds, it can lead to a beau- tiful and simple proof, which also “explains” why some- thing is true. In fact, I believe the search for an expla- nation, for understanding, is what we should really be aiming for. Proof is simply part of that process, and sometimes its consequence. As part of the search for new methods it is a good idea to broaden your horizons. Talking to people will extend your general education and will sometimes introduce you to new ideas and techniques. Very occa- sionally you may get a productive idea for your own research or even for a new direction. If you need to learn a new subject, consult the liter- ature but, even better, find a friendly expert and get instruction “from the horse’s mouth”—it gives more insight more quickly. As well as looking forward, and being alert to new developments, you should not forget the past. Many powerful mathematical results from earlier eras have got buried and have been forgotten, coming to light only when they have been independently rediscovered. These results are not easy to find, partly because ter- minology and style change, but they can be gold mines. As usual with gold mines, you have to be lucky to strike one, and the rewards go to the pioneers. Independence At the start of your research your relationship with your supervisor can be crucial, so choose carefully, bearing in mind subject matter, personality, and track record. Few supervisors score highly on all three. More- over, if things do not work out well during the first year or so, or if your interests diverge significantly, then do not hesitate to change supervisors or even universities. Your supervisor will not be offended and may even be relieved! Sometimes you may be part of a large group and may interact with other members of the faculty, so that you effectively have more than one supervisor. This can be helpful in that it provides different inputs and alterna- tive modes of work. You may also learn much from fel- low students in such large groups, which is why choos- ing a department with a large graduate school is a good idea. Once you have successfully earned your Ph.D. you enter a new stage. Although you may still carry on col- laborating with your supervisor and remain part of the same research group, it is healthy for your future devel- opment to move elsewhere for a year or more. This opens you up to new influences and opportunities. This is the time when you have the chance to carve out a niche for yourself in the mathematical world. In gen- eral, it is not a good idea to continue too closely in the line of your Ph.D. thesis for too long. You have to show your independence by branching out. It need not be a radical change of direction but there should be some clear novelty and not simply a routine continuation of your thesis. Style In writing up your thesis your supervisor will normally assist you in the manner of presentation and organi- zation. But acquiring a personal style is an important part of your mathematical development. Although the needs may vary, depending on the kind of mathemat- ics, many aspects are common to all subjects. Here are a number of hints on how to write a good paper. (i) Think through the whole logical structure of the paper before you start to write. (ii) Break up long complex proofs into short interme- diate steps (lemmas, propositions, etc.) that will help the reader. (iii) Write clear coherent English (or the language of your choice). Remember that mathematics is also a form of literature. (iv) Be as succinct as it is possible to be while remain- ing clear and easy to understand. This is a difficult balance to achieve. (v) Identify papers that you have enjoyed reading and imitate their style. (vi) When you have finished writing the bulk of your paper go back and write an introduction that explains clearly the structure and main results as well as the general context. Avoid unnecessary jar- gon and aim at a general mathematical reader, not just a narrow expert. � 1004 VIII. Final Perspectives (vii) Try out your first draft on a colleague and take heed of any suggestions or criticisms. If even your close friend or collaborator has difficulty under- standing it, then you have failed and need to try harder. (viii) If you are not in a desperate hurry to publish, put your paper aside for a few weeks and work on something else. Then return to your paper and read it with a fresh mind. It will read differently and you may see how to improve it. (ix) Do not hesitate to rewrite the paper, perhaps from a totally new angle, if you become convinced that this will make it clearer and easier to read. Well-written papers become “classics” and are widely read by future mathematicians. Badly writ- ten papers are ignored o