An Interview With Jean-Pierre Serre
By C.T. Chong and Y.K. Leong
National University of Singapore
Note: This article was first published in the June 1985
Issue of Mathematical Medley, a publication of the Singapore
Mathematical Society.
Jean-Pierre Serre was born in 1926 in France. He studied mathematics
at the Ecole Normale Superieure. In 1954, at the age of 28, he was
awarded a Fields Medal by the International Mathematical Union, the
highest recognition for achievement in mathematics. Two years later
he was appointed Professor of Algebra and Geometry at the College
de France, where for about 15 years he was the youngest professor.
He visited the Department of Mathematics, National University of
Singapore, from 2 to 15 February 1985. His visit was sponsored by
the French-Singapore Academic Exchange Programme. While in Singapore,
Professor Serre delivered two lectures on algebraic curves over
finite fields and one lecture on the Ramanujan function. He also
gave a two-hour seminar talk on Faltings' proof of the Mordell
conjecture, and a Colloquium lecture entitled "Discriminant =
b2 - 4ac" on class numbers of imaginary quadratic fields.
On February 14, 1985, he gave an interview in which he discussed
various aspects of his mathematical career and his views of
mathematics. What follows is a transcript of this interview,
edited by C.T. Chong and Y.K. Leong, and revised by J-P. Serre.
Q : What made you take up mathematics as your career?
A : I remember that I began to like mathematics when I was
perhaps 7 or 8. In high school I used to do problems for more
advanced classes. I was then in a boarding house in Nimes,
staying with children older than I was, and they used to bully me.
So to pacify them, I used to do their mathematics homework. It was
as good a training as any.
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.
Q : Did other subjects ever interest you, subjects like
physics and chemistry?
A : Physics not much, but chemistry yes. As I said, my parents
were pharmacists, so they had plenty of chemical products and
test-tubes. I played with them a lot when I was about 15 or 16
besides doing mathematics. And I read my father's chemistry books
(I still have one of them, a fascinating one, "Les Colloides" by
Jacques Duclaux). However, when I learned more chemistry, I got
disappointed by its almost mathematical aspect : there are long series
of organic compounds like CH4, C2H6,
etc, all looking more or less the same. I thought, if you have to
have series, you might as well do mathematics! So, I quit chemistry
- but not entirely : I ended up marrying a chemist.
Q : Were you influenced by any school teacher in doing
mathematics?
A : I had only one very good teacher. This was in my first
year in high school (1943-1944), in Nimes. He was nicknamed "Le
Barbu" : beards were rare at the time. He was very clear, and strict;
he demanded that every formula and proof be written neatly. And he
gave me a thorough training for the mathematics national competition
called "Concours General", where I eventually got first prize.
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!
Q : How important is inspiration in the discovery of
theorems?
A : I don't know what "inspiration" really means. Theorems,
and theories, come up in funny ways. Sometimes, you are just not
satisfied with existing proofs, and you look for better ones, which
can be applied in different situations. A typical example for me was
when I worked on the Riemann-Roch theorem (circa 1953), which I viewed
as an "Euler-Poincare" formula (I did not know then that
Kodaira-Spencer had had the same idea.) My first objective was to
prove it for algebraic curves - a case which was known for about a
century! But I wanted a proof in a special style; and when I managed
to find it, I remember it did not take me more than a minute or two
to go from there to the 2-dimensional case (which had just been done
by Kodaira). Six months later, the full result was established by
Hirzebruch, and published in his well-known Habilitationsschrift.
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.
Q : Have you ever had the experience where you found
a problem to be impossible to solve, and then after putting it aside
for some time, an idea suddenly occured leading to the solution?
A : Yes, of course this happens quite often. For instance,
when I was working on homotopy groups (~1950), I convinced myself
that, for a given space X, there should exist a fibre space E,
with base X, which is contractible; such a space would indeed allow
me (using Leray's methods) to do lots of computations on homotopy
groups and Eilenberg-MacLane cohomology. But how to find it? It
took me several weeks (a very long time, at the age I was then...)
to realize that the space of "paths" on X had all the necessary
properties - if only I dared call it a "fibre space", which I did.
This was the starting point of the loop-space method in algebraic
topology, many results followed quickly.
Q : Do you usually work on only one problem at a time or
several problems at the same time?
A : Mostly one problem at a time, but not always. And I work
often at night (in half-sleep), where the fact that you don't have
to write anything down gives to the mind a much greater concentration,
and makes changing topics easier.
Q : In physics, there are a lot of discoveries which were
made by accident, like X-rays, cosmic background radiation and so on.
Did that happen to you in mathematics?
A : A genuine accident is rare. But sometimes you get a surprise
because some argument you made for one purpose happens to solve a
question in a different direction; however, one can hardly call this
an "accident".
Q : What are the central problems in algebraic geometry or
number theory?
A : I can't answer that. You see, some mathematicians have
clear and far-ranging "programs". For instance, Grothendieck had such
a program for algebraic geometry; now Langlands has one for
representation theory, in relation to modular forms and arithmetic.
I never had such a program, not even a small size one. I just work on
things which happen to interest me at the moment. (Presently, the
topic which amuses me most is counting points on algebraic curves
over finite fields. It is a kind of applied mathematics : you try
to use any tool in algebraic geometry and number theory that you
know of ... and you don't quite succeed!)
Q : What would you consider to be the greatest developments
in algebraic geometry or number theory within the past five years?
A : This is easier to answer. Faltings' proof of the Mordell
conjecture, and of the Tate conjecture, is the first thing which
comes to mind. I would also mention Gross-Zagier's work on the
class number problem for quadratic fields (based on a previous theorem
of Goldfeld), and Mazur-Wiles theorem on Iwasawa's theory, using
modular curves. (The application of modular curves and modular
functions to number theory are especially exciting : you use GL2
to study GL1, so to speak! There is clearly a lot
more to come from that direction ... may be even a proof of the
Riemann Hypothesis some day!)
Q : Some scientists have done fundamental work in one field
and then quickly moved on to another field. You worked for three
years in topology, then took up something else. How did this happen?
A : It was a continuous path, not a discrete change. In 1952,
after my thesis on homotopy groups, I went to Princeton, where I
lectured on it (and on its continuation : "C-theory"), and attended
the celebrated Artin-Tate seminar on class field theory.
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 zetak(-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.
Q : What are the prospects of achieving some unification
of the diverse fields of mathematics?
A : I would say that this has been achieved already. I have
given above a typical example where Lie groups, number theory, etc,
come together, and cannot be separated from each other. Let me give
you another such example (it would be easy to add many more) :
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.
Q : How does one keep up with the explosion in mathematical
knowledge?
A : You don't really have to keep up. When you are interested
in a specific question, you find that very little of what is being
done has any relevance to you; and if something does have relevance,
then you learn it much faster, since you have an application in mind.
It is also a good habit to look regularly at Math. Reviews
(especially the collected volumes on number theory, group theory,
etc). And you learn a lot from your friends, too: it is easier to have
a proof explained to you at the blackboard, than to read it.
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.
Q : What do you think will be the impact of computers on
the development of mathematics?
A : Computers have already done a lot of good in some parts
of mathematics. In number theory, for instance, they are used in a
variety of ways. First, of course, to suggest conjectures, or
questions. But also to check general theorems on numerical examples
- which helps a lot with finding possible mistakes.
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.
Q : How could we encourage young people to take up
mathematics, especially in the schools?
A : I have a theory on this, which is that one should first
discourage people from doing mathematics; there is no need
for too many mathematicians. But, if after that, they still insist
on doing mathematics, then one should indeed encourage them, and
help them.
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).
Q : Would you say that the development of mathematics in
the past thirty years was faster than that in the previous thirty
years?
A : I am not quite sure this is true. The style is different.
In the 50's and 60's, the emphasis was quite often on general
methods : distributions, cohomology and the like. These methods
were very successful, but nowadays people work on more specific
questions (often, some quite old ones: for instance the classification
of algebraic curves in 3-dimensional projective spaces!). They
apply the tools which were made before; this is quite nice.
(And they also make new tools : microlocal analysis, supervarieties,
intersection cohomology...).
Q : In view of this explosion of mathematics, do you think
that a beginning graduate student could absorb this large amount of
mathematics in four, five or six years and begin original work
immediately after that?
A : Why not? For a given problem you don't need to know that
much, usually - and, besides, very simple ideas will often work.
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.
Q : In other words, one should aim at a problem first and
then learn whatever tools that are necessary for the problem?
A : Something like that. But since I know I cannot give
good advice to myself, I should not give advice to others. I don't
have a ready-made technique for working.
Q : You mentioned papers which have been forgotten. What
percentage of the papers published do you think will survive?
A : A non-zero percentage, I believe. After all, we still
read with pleasure papers by Hurwitz, or Eisenstein, or even Gauss.
Q : Do you think that you will ever be interested in the
history of mathematics?
A : I am already interested. But it is not easy; I do not
have the linguistic ability in Latin or Greek, for instance. And I
can see that it takes more time to write a paper on the history
of mathematics than in mathematics itself. Still, history is very
interesting; it puts things in the proper perspective.
Q : Do you believe in the classification of finite simple
groups?
A : More or less - and rather more than less. I would be amused
if a new sporadic group were discovered, but I am afraid this will
not happen.
More seriously, this classification theorem is a splendid thing. One
may now check many properties by just going through the list of
all groups (typical example : the classification of n-transitive
groups, for n at least 4).
Q : What do you think of life after the classification of
finite simple groups?
A : You are alluding to the fact that some finite group
theorists were demoralized by the classification; they said (or so
I was told) "there will be nothing more to do after that". I find
this ridiculous. Of course there would be plenty to do! First of
course, simplifying the proof (that's what Gorenstein calls
"revisionism"). But also finding applications to other parts of
mathematics; for instance, there have been very curious discoveries
relating the Griess-Fischer monster group to modular forms (the
so-called "Moonshine").
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.)
Q : But one would assume that most problems in mathematics
are like these, namely that the problems themselves may be difficult
and challenging, but after their solution they become useless.
In fact there are very few problems like the Riemann Hypothesis
where even before its solution, people already know many of its
consequences.
A : Yes, the Riemann Hypothesis is a very nice case: it
implies lots of things (including purely numerical inequalities,
for instance on discriminants of number fields). But there are
other such examples : Hironaka's desingularization theorem is one;
and of course also the classification of finite simple groups we
discussed before.
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.
Q : Do you still go back to problems in topology?
A : No. I have not kept track of the recent techniques, and
I don't know the latest computations of the homotopy groups of
spheres pin+k(Sn) (I guess people have
already reached up to k=40 or 50. I used to know them up to k=10
or so.)
But I still use ideas from topology in a broad sense, such as
cohomology, obstructions, Stiefel-Whitney classes, etc.
Q : What has been the influence of Bourbaki on mathematics?
A : A very good one. I know it is fashionable to blame
Bourbaki for everything ("New Math" for instance), but this is unfair.
Bourbaki is not responsible. People just misused his books; they
were never meant for university teaching, even less high school
teaching.
Q : Maybe a warning sign should have been given?
A : Such a sign was indeed given by Bourbaki : it is the
Seminaire Bourbaki. The seminaire is not at all formal like the
books; it includes all sorts of mathematics, and even some physics.
If you combine the seminaire and the books, you get a much more
balanced view.
Q : Do you see a decreasing influence of Bourbaki on
mathematics?
A : The influence is different from what it was. Forty years
ago, Bourbaki had a point to make; he had to prove that an
organized and systematic account of mathematics was possible. Now
the point is made and Bourbaki has won. As a consequence, his
books now have only technical interest; the question is just
whether they give a good exposition of the topic they are on.
Sometimes they do (the one on "root systems" has become standard
reference in the field); sometimes they don't (I won't give an
example : it is too much a matter of taste).
Q : Speaking of taste, can you say what kind of style
(for books, or papers), you like most?
A : Precision combined with informality! That is the ideal,
just as it is for lectures. You find this happy blend in authors
like Atiyah or Milnor, and a few others. But it is hard to achieve.
For instance, I find many of the French (myself included) a bit
too formal, and some of the Russians a bit too imprecise...
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".
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