An Interview with Jean-Pierre Serre

My mother was a pharmacist (as was my father), and she liked mathematics. When she was a pharmacy student, at the University of Montpellier, she had taken a first-year course in calculus, just for fun, and passed the exam. And she had carefully kept her calculus books (by Fabry and Vogt, if I remember correctly). When I was 14 or 15, I used to look at these books, and study them. This is how I learned about derivatives, integrals, series and such (I did that in a purely formal manner -- Euler's style so to speak: I did not like, and did not understand, epsilons and deltas.) At that time, I had no idea one could make a living by being a mathematician. It was only later I discovered one could get paid for doing mathematics! What I thought at first was that I would become a high school teacher: this looked natural to me. Then, when I was 19, I took the competition to enter the Ecole Normale Superieure, and I succeeded. Once I was at "I'Ecole", it became clear that it was not a high school teacher I wanted to be, but a research mathematician.

Speaking of Concours General, I also tried my hand at the one in physics, the same year (1944). The problem we were asked to solve was based entirely on some physical law I was supposed to know, but did not. Fortunately, only one formula seemed to me possible for that law. I assumed it was correct, and managed to do the whole 6-hour problem on that basis. I even thought I would get a prize. Unfortunately, my formula was wrong, and I got nothing -- as I deserved!

Quite often, you don't really try to solve a specific question by a head-on attack. Rather you have some ideas in mind, which you feel should be useful, but you don't know exactly for what they are useful. So, you look around, and try to apply them. It's like having a bunch of keys, and trying them on several doors.

Then, I returned to Paris, where the Cartan seminar was discussing functions of several complex variables, and Stein manifolds. It turned out that the recent results of Cartan-Oka could be expressed much more efficiently (and proved in a simpler way) using cohomology and sheaves. This was quite exciting, and I worked for a short while on that topic, making applications of Cartan theory to Stein manifolds. However, a very interesting part of several complex variables is the study of projective varieties (as opposed to affine ones -- which are somewhat pathological for a geometer); so, I began working on these complex projective varieties, using sheaves: that's how I came to the circle of ideas around Riemann-Roch, in 1953. But projective varieties are algebraic (Chow's theorem), and it is a bit unnatural to study these algebraic objects using analytic functions, which may well have lots of essential singularities. Clearly, rational functions should be enough -- and indeed they are. This made me go (around 1954) into "abstract" algebraic geometry, over any algebraically closed field. But why assume the field is algebraically closed? Finite fields are more exciting, with Weil conjectures and such. And from there to number fields it is a natural enough transition ... This is more or less the path I followed.

Another direction of work came from my collaboration (and friendship) with Armand Borel. He told me about Lie groups, which he knows like nobody else. The connections of these groups with topology, algebraic geometry, number theory, ... are fascinating. Let me give you just one such example (of which I became aware about 1968):

Consider the most obvious discrete subgroup of SL₂(R), namely G = SL₂(Z). One can compute its "Euler-Poincare characteristic" X(G) which turns out to be -1/12 (it is not an integer: this is because G has torsion). Now -1/12 happens to be the value zeta(-1) of the Riemann's zeta-function at the point s = -1 (a result known already to Euler). And this is not a coincidence! It extends to any totally real number field K, and can be used to study the denominator of zeta_k(-1). (Better results can be obtained by using modular forms, as was found later.) Such questions are not group theory, nor topology, nor number theory: they are just mathematics.

There is a beautiful theorem proved recently by S. Donaldson on four-dimensional compact differentiable manifolds. It states that the quadratic form (on H²) of such a manifold is severely restricted; if it is positive definite, it is a sum of squares. And the crux of the proof is to construct some auxiliary manifold (a "cobordism") as the set of solutions of some partial differential equation (non linear, of course)! This is a completely new application of analysis to differential topology. And what makes it even more remarkable is that, if the differentiability assumption is dropped, the situation becomes quite different: by a theorem of M. Freedman, the H²-quadratic form can then be almost anything.

A more serious problem is the one on the "big theorems" which are both very useful and too long to check (unless you spend on them a sizable part of your lifetime...). A typical example is the Feit-Thompson Theorem: groups of odd order are solvable. (Chevalley once tried to take this as the topic of a seminar, with the idea of giving a complete account of the proof. After two years, he had to give up.) What should one do with such theorems, if one has to use them? Accept them on faith? Probably. But it is not a very comfortable situation.

I am also uneasy with some topics, mainly in differential topology, where the author draws a complicated picture (in 2 dimensions), and asks you to accept it as a proof of something taking place in 5 dimensions or more. Only the experts can "see" whether such a proof is correct or not -- if you can call this a proof.

They are also very useful when there is a large search to be made (for instance, if you have to check 10⁶ or 10⁷ cases). A notorious example is the proof of the Four-Colour Theorem. There is however a problem there, somewhat similar to the one with Feit-Thompson: such a proof cannot be checked by hand; you need a computer (and a very subtle program). This is not very comfortable either.

As for high school students, the main point is to make them understand that mathematics exists, that it is not dead (they have a tendency to believe that only physics, or biology, has open questions). The defect in the traditional way of teaching mathematics is that the teacher never mentions these questions. It is a pity. There are many such, for instance in number theory, that teenagers could very well understand: Fermat of course, but also Goldbach, and the existence of infinitely many primes of the form n² + 1. And one should also feel free to state theorems without proving them (for instance Dirichlet's theorem on primes in arithmetic progression).

Some theories get simplified. Some just drop out of sight. For instance, in 1949, I remember I was depressed because every issue of Annals of Mathematics would contain another paper on topology which was more difficult to understand than the previous ones. But nobody looks at these papers any more; they are forgotten (and deservedly so: I don't think they contained anything deep ...). Forgetting is a very healthy activity.

Still, it is true that some topics need much more training than some others, because of the heavy technique which is used. Algebraic geometry is such a case; and also representation theory.

Anyway, it is not obvious that one should say "I am going to work in algebraic geometry", or anything like that. For most people, it is better to just follow seminars, read things, and ask questions to oneself; and then learn the amount of theory which is needed for these questions.

It is just like asking whether Faltings' proof of the Mordell conjecture killed the theory of rational points on curves. No! It is merely a starting point. Many questions remain open.

(Still, it is true that sometimes a theory can be killed. A well-known example is Hilbert's fifth problem: to prove that every locally euclidean topological group is a Lie group. When I was a young topologist, that was the problem I really wanted to solve -- but I could get nowhere. It was Gleason, and Montgomery-Zippin, who solved it, and their solution all but killed the problem. What else is there to find in this direction? I can think of one question: can the group of p-adic integers act effectively on a manifold? This seems quite hard -- but a solution would have no application whatsoever, as far as I can see.)

Sometimes it is the method used in the proof which has lots of applications: I am confident this will happen with Faltings. And sometimes, it is true, the problems are not meant to have applications; they are a kind of test on the existing theories; they force us to look further.

But I still use ideas from topology in a broad sense, such as cohomology, obstructions, Stiefel-Whitney classes, etc.

A further point I want to make is that papers should include more side remarks, open questions, and such. Very often, these are more interesting than the theorems actually proved. Alas, most people are afraid to admit that they don't know the answer to some question, and as a consequence they refrain from mentioning the question, even if it is a very natural one. What a pity! As for myself, I enjoy saying "I do not know".