- Date:
- From:
- Michael Atiyah et al.
- To:
- Giung Nam
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Advice to a young mathematician
- Source:
Selected excerpts from five contributions in The Princeton Companion to Mathematics (2008). Omissions are marked with […].
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 characteristics and you should follow your own instinct. You may 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.
[…]
The Role of Curiosity
The driving force in research is curiosity. When is a particular 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 possible 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 knowing 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 listening to a lecture where the result is beautiful and the proof ugly and complicated. Instead of trying to follow a messy proof on the blackboard, I spend the rest of the hour thinking about producing a more elegant 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.
[…]
II. Béla Bollobás
I would recommend that at any one time you have problems of two types to work on.
(i) A “dream”: a big problem that you would love to solve, but you cannot reasonably expect to solve.
(ii) Some very worthwhile problems that you feel you should have a good chance of solving, given enough time, effort, and luck.
[…]
Do not be afraid to make mistakes. A mistake for a chess player is fatal; for a mathematician it is par for the course. What you should be terrified of is a blank sheet in front of you after having thought about a problem for a little while. If after a session your wastepaper basket is full of notes of failed attempts, you may still be doing very well. Avoid pedestrian approaches, but always be happy to put in work. In particular, doing the simplest cases of a problem is unlikely to be a waste of time and may well turn out to be very useful.
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III. Alain Connes
Being brave. There are several phases in the process that leads to the discovery of new mathematics. While the checking phase is scary, but involves just rationality and concentration, the first, more creative, phase is of a totally different nature. In some sense, it requires a kind of protection of one’s ignorance, since this also protects one from the billions of reasons there will always be for not looking at a problem that has already been unsuccessfully attacked by many other mathematicians.
[…]
Grudging approbation. A colleague of mine once said, “We [mathematicians] work for the grudging approbation of a few friends.” It is true that, since research work is of a rather solitary nature, we badly need that approbation in one way or another, but quite frankly one should not expect much. In fact, the only real judge is oneself. Nobody else is in as good a position to know what work was involved, and caring too much about the opinion of others is a waste of time: so far no theorem has been proved as the result of a vote. As Feynman put it, “Why do you care what other people think?”
IV. Dusa McDuff
I probably most needed to learn how to ask good questions. As a student, one’s job is not only to learn enough to be able to answer questions posed by others, but also to learn how to frame questions that might lead somewhere interesting. When studying something new I often used to start in the middle, using some complicated theory already developed by others. But often one sees further by starting with the simplest questions and examples, because that makes it easier to understand the basic problem and then perhaps to find a new approach to it. For example, I have always liked working with Gromov’s nonsqueezing theorem in symplectic geometry, which imposes restrictions on the ways a ball can be manipulated in a symplectic way. This very fundamental and geometric result somehow resonates for me, and so forms a solid basis from which to start exploring.
These days people are much more aware that mathematics is a communal endeavor: even the most brilliant idea gets meaning only from its relation to the whole. Once one has an understanding of the context, it is often very important and fruitful to work by oneself. However, while one is learning it is vital to interact with others.
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V. Peter Sarnak
(i) When learning an area, one should combine reading modern treatments with a study of the original papers, especially papers by the masters of our subject. One of the troubles with recent accounts of certain topics is that they can become too slick. As each new author finds cleverer proofs or treatments of a theory, the treatment evolves toward the one that contains the “shortest proofs.” Unfortunately, these are often in a form that causes the new student to ponder, “How did anyone think of this?” By going back to the original sources one can usually see the subject evolving naturally and understand how it has reached its modern form. (There will remain those unexpected and brilliant steps at which one can only marvel at the genius of the inventor, but there are far fewer of these than you might think.) As an example, I usually recommend reading Weyl’s original papers on the representation theory of compact Lie groups and the derivation of his character formula, alongside one of the many modern treatments. Similarly, I recommend his book The Concept of a Riemann Surface to someone who knows complex analysis and wants to learn about the modern theory of Riemann surfaces, which is of central importance to many areas of mathematics. It is also instructive to study the collected works of superb mathematicians such as Weyl. Besides learning their theorems one uncovers how their minds work. There is almost always a natural line of thought that leads from one paper to the next and certain developments are then appreciated as inevitable. This can be very inspiring.
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