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.
Dear Sowa,
ReplyDeleteIndeed, my question was vague but your answer was interesting as always. When your thoughts flow freely they produce beautiful little gems that make your blog such an interesting read. Perhaps, to make my question more specific... Looking back at your career and the development of mathematics around you, what advice would you give to people early in their career? What do you know now that you could not anticipate at the beginning of your career?
Smorinsky's prediction may be too optimistic. I often think that people who work in a given area almost on purpose make it inaccessible to others, using heavy jargon, folklore lemmas without proofs, poor referencing. It is almost impossible to navigate through this mess, unless you are guided by insiders. They prefer to act as a monopoly and are not really interested in explaining trade secrets to outsiders. This may serve many purposes. For example, I read an article published a few years ago by some very famous people in one of the best journals that exaggerated their contribution to an almost laughable degree. They could do this because not many people know about the problem and what are the important issues. In this case, I happened to know the facts, but it made me wonder how many other "great ideas" produced by these people are not really that great.
Dear Tamas Gabal,
ReplyDeleteI am very glad that you appreciate this style of writing. I hope that it is not yet a fully developed stream of consciousness.
Smorinsky prediction was based on the observation that this was needed. It is much more needed now than it was in the 1980ies. Still, nobody does this. Actually, I do not remember precisely how it was stated: as a prediction or as a natural thing to do and therefore something to expect. But now mathematicians are under a heavy pressure to produce publications, and expository publications do not count when key decisions are made. Young people need to get a permanent (tenure-track) position. Then they need to get tenure. If you look at the lists of publications and CV’s of people who got tenure around 1980, you will see that many published just 3-4 papers before the tenure decision. Now a postdoc is expected to publish 3-4 research papers a year. Nobody teaches young people how to write mathematics. I was very happy: my advisor spent a lot of time teaching me how to write. Of course, he did not teach me to write in the style of this blog. Mathematics should be written completely differently.
I doubt that many write in an obscure manner out of some malicious intent. They just don’t know how, and nobody cares. As a result we indeed have a lot of mess and a lot of areas impenetrable for the outsiders. Well, they will pay for this mess themselves. An oral tradition rarely survives for more than two generations. Then their results will be lost. I think that many results are lost already despite their discoverers are around and could be even active.
But you are right, the significance of many results is exaggerated, and an obscure exposition helps to hide the truth. The starting point of this blog, the Szemerédi theorem, is a good example. I was told by real experts that his paper with the proof is unreadable. So, Gowers and people around him do not afraid of saying that Szemerédi is a genius. Furstenberg’s proof, which is very accessible, was initially ignored, and later, already in this millennium, combined with the Szemerédi’s one. There is a branch of my beloved algebraic geometry which is closed for outsiders. 3 Fields medals went to mathematicians working in this area. 2 of these 3 medalists had the same thesis advisor. Well, it is very unlikely that I will ever have a firsthand opinion about their works. While I am sure that their work is incomparably deeper than anything done by Gowers, Tao, Szemerédi, and cannot compare it with much more accessible achievements of other algebraic geometers or algebraists.
Your first question is much more difficult because by giving an advice I will assume some responsibility. About a year ago somebody with nickname “Flora” posted a question on mathoverflow seeking a similar advice. By that time Flora already had some problems with his or her life in the mathematical community, and the question was like “in your opinion, can I still do mathematics”. In the answers, especially in the top voted answer, my fellow mathematicians decided to show their worst side. More or less they said “since you are asking such questions, get out now”. For a year I was thinking about writing a more realistic and decent reply to Flora. The problem is that Flora left no way to contact him or her. The question was “closed”, meaning that no more answers can be posted. And the moderators of this community really hate any general discussion even of the type “is it indeed likely that A solved the problem B, as claimed?” How Flora will learn about my answer even if I write it down?
ReplyDeleteBut now you are asking not the same question, but a close one. It looks like I may use my tentative answer to Flora. May be this is indeed the case, but I need to ask you to be still more specific in order to be sure. In addition, a year passed.
A lot of unpleasant things happened during this year. For example, Gowers spoke about Deligne works which are well beyond his comprehension. By now it is completely clear that Gowers and a big community of software engineers are working on elimination of mathematics. They will succeed only if Gowers succeeds in replacing the conceptual mathematics by the Hungarian one. His achievements in this direction during the past 10 years are truly remarkable.
How can I give any advice about entering a profession which may disappear in 25 years with probability 10%, and in 40 years – with probability 50%? These are estimates of Gowers himself. He gives mathematics only 10% chances of surviving till the end of the century.
I will a little bit about my experience later.
"There is a branch of my beloved algebraic geometry which is closed for outsiders. 3 Fields medals went to mathematicians working in this area" can you please throw some light on this branch of Algebraic Geometry ?
ReplyDeleteDear Ravi,
ReplyDeleteWell, I am not an insider. I thought this is clear from that I wrote. Of course, there are some expositions, say, in the Proceedings of Congresses. There are some expository papers in Bull. AMS. One can study some related things, like elliptic modules, and some algebraic number theory, and come to some conclusions by "analytic continuation". One can go to, say, Paris, and study this area. But I lack motivation for such drastic changes in my life. Who will pay me for a couple years in Paris?
Dear Sowa,
ReplyDeleteI tried to imagine how Deligne must have felt about the Gowers presentation of his work and all I can picture is his amused smile. On the one hand, you are right, the award of such magnitude is not only a celebration of one person but the whole area, and such occasion deserves a presentation by an expert who understands the subtlety and beauty of ideas involved. On the other hand, in some strange way, we can interpret this as a complement to Deligne.
I do not look for any specific career advice, but I just want to know your opinion on the issues that are important to you. Something that might not be so obvious to a young person. For example, you mentioned that the problems are often solved by methods developed for completely different purposes. This can be interpreted in two different ways. First - if you work on some problem, you should constantly look for ideas that may seem unrelated to apply to your problem. Second - focus entirely on the development of your ideas and look for problems that may seem unrelated to apply your ideas. I personally lean toward the latter, but your advice may be different. This is just an example, but I am interested in any thoughts from experience.
Dear Tamas Gabal,
ReplyDeleteI don’t think that this was a compliment. But I don’t think that Deligne felt offended. Decades ago Deligne reached the point when a prize awarded to him does not increase his stature in the community. An award to Deligne increases the stature of the prize. This award increases the stature of the Abel prize, and, as a corollary, the stature of E. Szemerédi and of Szemerédi-Gowers type of mathematics. The fact that Gowers was presenting the works of Deligne magnifies this effect by at least an order of magnitude. (The statement about the order of magnitude can be made precise, which is a little bit surprising.)
For my reply to your second paragraph, please see About some ways to work in mathematics.