New ideas

Previous post: Did J. Lurie solved any big problem?


Tamas Gabal asked:

“Dear Sowa, in your own experience, how often genuinely new ideas appear in an active field of mathematics and how long are the periods in between when people digest and build theories around those ideas? What are the dynamics of progress in mathematics, and how various areas are different in this regard?”

Here is my partial reply.


This question requires a book-length answer; especially because it is not very precisely formulated. I will try to be shorter. :- )

First of all, what should be considered as genuinely new ideas? How new and original they are required to be? Even for such a fundamental notion as an integral there are different choices. At one end, there is only one new idea related to it, which predates the discovery of the mathematics itself. Namely, it is idea of the area. If we lower our requirements a little, there will be 3 other ideas, associated with the works or Archimedes, Lebesque, and hardly known by now works of Danjoy, Perron, and others. The Riemann integral is just a modern version of Archimedes and other Ancient Greek mathematician. The Danjoy integral generalizes the Lebesgue one and has some desirable properties which the Lebesgue integral has not. But it turned out to be a dead end without any applications to topics of general interest. I will stop my survey of the theory of integration here: there are many other contributions. The point is that if we lower our requirements further, then we have much more “genuinely new” ideas.

It would be much better to speak not about some vague levels of originality, but about areas of mathematics. Some ideas are new and important inside the theory of integration, but are of almost no interest for outsiders.

You asked about my personal experience. Are you asking about what my general knowledge tells me, or what happened in my own mathematical life? Even if you are asking about the latter, it is very hard to answer. At the highest level I contributed no new ideas. One may even say that nobody after Grothendieck did (although I personally believe that 2 or 3 other mathematicians did), so I am not ashamed. I am not inclined to classify my work as analysis, algebra, geometry, topology, etc. Formally, I am assigned to one of these boxes; but this only hurts me and my research. Still, there is a fairly narrow subfield of mathematics to which I contributed, probably, 2 or 3 ideas. According to A. Weil, if a mathematician had contributed 1 new idea, he is really exceptional; most of mathematicians do not contribute any new ideas. If a mathematician contributed 2 or 3 new ideas, he or she would be a great mathematician, according to A. Weil. By this reason, I wrote “2 or 3” not without a great hesitation. I do not overestimate myself. I wanted to illustrate what happens if the area is sufficiently narrow, but not necessarily to the limit. The area I am taking about can be very naturally partitioned further. I worked in other fields too, and I hope that these papers also contain a couple of new ideas. For sure, they are of a level lower than the one A. Weil had in mind.

On one hand side this personal example shows another extreme way to count the frequency of new ideas. I don’t think that it would be interesting to lower the level further. Many papers and even small lemmas contain some little new ideas (still, much more do not). On the other side, this is important on a personal level. Mathematics is a very difficult profession, and it lost almost all its appeal as a career due to the changes of the universities (at least in the West, especially in the US). It is better to know in advance what kind of internal reward you may get out of it.

As of the timeframe, I think that a new idea is usually understood and used within a year (one has to keep in mind that mathematics is a very slow art) by few followers of the discoverer, often by his or her students or personal friends. Here “few” is something like 2-5 mathematicians. The mathematical community needs about 10 years to digest something new, sometimes it needs much more time. It seems that all this is independent of the level of the contribution. The less fundamental ideas are of interest to fewer people. So they are digested more slowly, despite being easier.

I don’t have much to say about the dynamics (what is the dynamics here?) of progress in mathematics. The past is discussed in many books about history of mathematics; despite I don’t know any which I could recommend without reservations. The only exception is the historical notes at the ends of N. Bourbaki books (they are translated into English and published as a separate book by Springer). A good starting point to read about 20th century is the article by M. Atiyah, “Mathematics in the 20th century”, American Mathematical Monthly, August/September 2001, p. 654 – 666. I will not try to predict the future. If you predict it correctly, nobody will believe you; if not, there is no point. Mathematicians usually try to shape the future by posing problems, but this usually fails even if the problem is solved, because it is solved by tools developed for other purposes. And the future of mathematics is determined by tools. A solution of a really difficult problem often kills an area of research, at least temporarily (for decades minimum).

My predictions for the pure mathematics are rather bleak, but they are based on observing the basic trends in the society, and not on the internal situation in mathematics. There is an internal problem in mathematics pointed out by C. Smorinsky in the 1980ies. The very fast development of mathematics in the preceding decades created many large gaps in the mathematical literature. Some theories lack readable expositions, some theorem are universally accepted but appear to have big gaps in their proofs. C. Smorinsky predicted that mathematicians will turn to expository work and will clear this mess. He also predicted more attention to the history of mathematics. A lot of ideas are hard to understand without knowing why and how they were developed. His predictions did not materialize yet. The expository work is often more difficult than the so-called “original research”, but it is hardly rewarded.


Next post: About some ways to work in mathematics.

A reply to some remarks by André Joyal

Previous post: The first post.


I am a fairly surprised by your criticism of Bourbaki work (I would be not surprised by a critique of Bourbaki from many other mathematicians). I hardly can say anything new in the defense of Bourbaki. The best defense was, probably, provided by J. Dieudonne. And one should not forget that, as some other former member of Bourbaki pointed out, that Bourbaki books succeeded in changing the style in which books in mathematics are written. There is no more such an urgent need in rigorous and systematic expositions as was in France before WWII, because many books by other authors are both rigorous and systematic.

Of course, applications are absent from Bourbaki books, as they are absent from almost all books in pure mathematics. I doubt that I ever read or used any book in pure mathematics discussing applications. And since I think that pure mathematics is not needed for any applications, I believe that it is better to separate them.

The issue of the presumed absence of motivation in Bourbaki books is more subtle. There are several sorts of motivations. A reference to applications is a common but very poor motivation to study proofs, because only statements and formulas are needed for applications. It seems that the most widespread sort of motivation is a pseudo-historical one: one invents some way how mathematicians could in principle arrive at a result or definition; in the best cases it resembles the actual history. Very often such a motivation uses tools developed only later and, moreover, under the influence of the original discovery. I consider such motivations as very misleading. The only true motivation in mathematics is the real history of the problem or of the theory at hand. I learned this point of view from my Ph.D. thesis adviser in the context of writing introductions to research papers, and later I saw that it applies to expository writings, textbooks, everywhere. Using it in the teaching or learning is possible, but by purely practical reasons only occasionally. This approach requires such amount of time that it will defer own research by decades. Another effective form of motivation is apparently already forgotten in the western countries. It is simply the trust to a more experienced person than you. If you are told that you will need to know the derived categories or it just worth to know about them, this should be a sufficient motivation and you will study the theory of derived categories. Finally, the organization of the material could be self-motivating. I think that Bourbaki books are superb in this respect. They are, in fact, much more readable than most of mathematicians think. Many other books are also self-motivating without any special efforts.


Next post: The times of André Weil and the times of Timothy Gowers. 1.