Tamas Gabal asked the following question.
I heard a criticism of Lurie's work, that it does not contain startling new ideas, complete solutions of important problems, even new conjectures. That he is simply rewriting old ideas in a new language. I am very far from this area, and I find it a little disturbing that only the ultimate experts speak highly of his work. Even people in related areas can not usually give specific examples of his greatness. I understand that his objectives may be much more long-term, but I would still like to hear some response to these criticisms.
Short answer: I don't care. Here is a long answer.
Well, this is the reason why my opinion about Lurie is somewhat conditional. As I already said, if an impartial committee confirms the significance of Lurie’s work, it will remove my doubts and, very likely, will stimulate me to study his work in depth. It is much harder to predict what will be the influence of the actual committee. Perhaps, I will try to learn his work in any case. If he will not get the medal, then in the hope to make sure that the committee is wrong.
I planned to discuss many peculiarities of mathematical prizes in another post, but one of these peculiarities ought to be mentioned now. Most of mathematical prizes go to people who solved some “important problems”. In fact, most of them go to people who made the last step in solving a problem. There is recent and famous example at hand: the Clay $1,000,000.00 prize was awarded to Perelman alone. But the method was designed by R. Hamilton, who did a huge amount of work, but wasn’t able to made “the last step”. Perhaps, just because of age. As Perelman said to a Russian news agency, he declined the prize because in his opinion Hamilton’s work is no less important than his own, and Hamilton deserves the prize no less than him. It seems that this reason still not known widely enough. To the best of my knowledge, it was not included in any press-release of the Clay Institute. The Clay Institute scheduled the award ceremony like they knew nothing, and then held the ceremony as planned. Except Grisha Perelman wasn’t present, and he did not accept the prize in any sense.
So, the prizes go to mathematicians who did the last step in the solution of a recognized problem. The mathematicians building the theories on which these solutions are based almost never get Fields medals. Their chances are more significant when prize is a prize for the life-time contribution (as is the case with the Abel prize). There are few exceptions.
First of all, A. Grothendieck is an exception. He proved part of the Weil conjectures, but not the most important one (later proved by P. Deligne). One of the Weil conjectures (the basic one) was independently proved by B. Dwork, by a completely different and independent method, and published earlier (by the way, this is fairly accessible and extremely beautiful piece of work). The report of J. Dieudonne at the 1966 Congress outlines a huge theory, to a big extent still not written down then. It includes some theorems, like the Grothendieck-Riemann-Roch theorem, but: (i) GRR theorem does not solve any established problem, it is a radically new type of a statement; (ii) Grothendieck did not published his proof, being of the opinion that the proof is not good enough (an exposition was published by Borel and Serre); (iii) it is just a byproduct of his new way of thinking.
D. Quillen (Fields medal 1978) did solve some problems, but his main achievement is a solution of a very unusual problem: to give a good definition of so-called higher algebraic K-functors. It is a theory. Moreover, there are other solutions. Eventually, it turns out that they all provide equivalent definitions. But Quillen’s definitions (actually, he suggested two) are much better than others.
So, I do not care much if Lurie solved some “important problems” or not. Moreover, in the current situation I rather prefer that he did not solved any well-known problems, if he will get a Fields medal. The contrast with the Hungarian combinatorics, which is concentrated on statements and problems, will make the mathematics healthier.
Problems are very misleading. Often they achieve their status not because they are really important, but because a prize was associated with them (Fermat Last Theorem), or they were posed by a famous mathematicians. An example of the last situation is nothing else but the Poincaré Conjecture – in fact, Poincaré did not stated it as a conjecture, he just mentioned that “it would be interesting to know the answer to the following question”. It is not particularly important by itself. It claims that one difficult to verify property (being homeomorphic to a 3-sphere) is equivalent to another difficult to verify property (having trivial fundamental group). In practice, if you know that the fundamental group is trivial, you know also that your manifold is a 3-sphere.
Next post: New ideas.
Sowa, despite the provocative nature of your words, I agree with you. On the other hand, perhaps, the hands of the Fields Committee are tied and they have to select the big-problem-solvers. But this is exactly the argument against the Fields medal.
ReplyDeleteDear Tamas Gabal,
ReplyDeleteI intentionally write in a provocative manner quite often. This is the result of observing the online reaction to unconventional ideas of many people, including my. I decided to keep the current title of this blog much longer than I initially planned by similar reasons.
The word "provocative" doesn't seem to be a purely negative characteristic. I would like to provoke thinking.
This was about the style; let us go to the substance.
What do you mean by saying the "the hands of the Fields Committee are tied"? It seems that the only function of this Committee is to execute (the relevant part of) the Fields will. There is nothing there about big-problem-solvers.
I tried to illustrate by examples that some medals went to theory-builders. There are other examples. I wanted to add them to the post, but let me mention them here. First, Laurent Schwartz (1950) for the theory of distributions. This a pure theory-building. By the way, I highly recommend his autobiography and especially the chapter about the theory of distributions.
And I missed V. Drinfeld (1990). He was indirectly mentioned in a previous post. Some people concluded that I "have something agains him". I don't. What is important in the current context is that he is a theory-builder. The presentation of his work by Yu. Manin at the Congress clearly indicates what was (and is) valued in his work. (Amazingly, my top choice for the medal in 1990 was and still is a mathematician who appeared at the time to be a problem-solver.)
Dear Sowa, in my opinion, the most provocative sentence in your post was: "Moreover, in the current situation I rather prefer that he did not solve any well-known problems, if he will get a Fields medal." It almost sounds like a challenge! Also, I meant that the hand of the Committee are tied in the same sense as you described - it is a part of modern mathematical culture that "most of mathematical prizes go to people who solved some important problems", which is probably due to the human nature more than anything else. And Committee members are human too.
ReplyDeleteI am fascinated by the way you talk about the role of definitions in a radical new way of thinking. There must be some developments, perhaps based on reflection on open problems, from which these new insights emerge? How else do you explain their origin?
Based on your other posts, your first choice in 1990 would also be eligible in 1994?
Well, may be it is provocative. I just stated my preferences, and, moreover, preferences not intrinsic to the mathematics. But for whom this could be challenge? Lurie did what he did. Even if he proves Riemann Hypothesis next week, there will be no time to verify his solution before 2014 Congress. It is definitely not a challenge for Lurie.
ReplyDeleteProbably, it is a challenge for the Committee: are you able to appreciate a piece of mathematics without having applications to famous problems at your disposal? In other words, are you competent enough to execute the Fields will? Fields wanted not only to reward the work done, but also to stimulate further work. If a new theory by a medalist holds a promise to solve some problem after being fully developed, then we have a good occasion to stimulate the continuation of the work. I should say that, in fact, I hardly believe that scientific prizes very rarely stimulate people to do anything, but there are exceptions and a lot of people think that they do. The main purpose of prizes (it does not matter if they are funded privately or by a government) is to get access to the taxpayers’ money.
Up to now, the Fields Medal committees were not particularly successful with this part of the Fields will. Almost all Fields medalists did their best work before the award; many ceased to work immediately after. The most stupid aspect of the prize (to be provocative, I should say “idiotic beyond comprehension”), the 40 years rule, was somehow derived from this phrase in the will.
My top choice for 1990 was not eligible in 1994, he turned 40 by 1994.
The Committee hands are not tied in the sense you described. In fact, the previous committees are themselves responsible for this cult of “Big Famous Problems”. To a big extend they created it. The future committees are in position to at least start dismantling it. Of course, there are many other reasons for this cult also (for example, the mathematical Olympiads, which gradually turned away from their original purpose).
In addition, solving some problem is an inevitable test for new ideas. Nobody is interested in a complicated theory build dealing only with its own problems. I have nothing against solving problems, big or small. I am against turning solving the problems into the main criterion of a mathematician’s worth. For example, H. Grassmann did not solve any famous problem; I think that he did not solve any explicitly stated problem at all. And his work is one of the most important works done in 19th century. His main contribution is a definition, namely the definition of the Grassmann algebra. Now we hardly can live without it.
The example of Grassmann shows that it is more or less impossible to explain how mathematician arrive at new definitions. They do this in a lot of different ways. Sometimes they do this in the process of solving a problem. But usually a really deep specific problem is solved only when all necessary definitions are already in place. A good problem leading to new definitions is usually not a precisely formulated problem like the Last Fermat Theorem. It is an “open problem” of the kind Poincaré preferred. Some examples: “to find a good extension of Riemann’s definition of an integral to a wider class of functions”; “to find a good definition of higher algebraic K-functors” (note that before this problem is “solved”, one cannot even say about what it is).
Sowa, do you believe that what makes a part of math "conceptual" are only and ultimately definitions? Because I believe that techniques can themselves be conceptual. For example (and in contrast to your depiction of Hungarian combinatorics as antithetical to conceptual math), I see the probabilistic method as a conceptual advance. Its main content- that in order to show a configuration meeting particular constraints is achievable, it suffices to show that a random configuration meets these constraints with positive probability- is more-or-less tautological. Nevertheless, the probabilistic method completely changes one's perspective on how to approach these sorts of combinatorial problems.
ReplyDeleteDear shopkins,
ReplyDeleteFirst of all, I do not believe anymore that mathematics can be divided into "two cultures" of T. Gowers. I wrote about this already. A branch of mathematics can be more or less conceptual, like it can be more geometrical (i.e. based on the spatial intuition), or less geometrical. "Hungarian combinatorics" is a widely used phrase, describing an extremely anticonceptual tradition, apparently the most anticonceptual one.
Of course, it is the definitions what makes a branch of mathematics conceptual. This is a tautology, more or less: concepts are introduced by their definitions, except initially definitions may be only tentative.
It is very hard for me to consider the probabilistic method as conceptual. I even think that the word “probabilistic” is intentionally misleading. To the best of my knowledge, no real probability theory is involved. It is just counting. If the total number of possible configuration is less than the sum of numbers of configurations satisfying properties A and B, there is a configuration satisfying both A and B. I doubt that this idea may be considered as a recent advance. 10,000 years ago – may be.
Probabilistic method does not change the perspective on how to approach some problems. It changes the perspective on what papers are publishable. Before, one should be able to construct a configuration (ideally, to give a full description of them). After, one may be happy by proving just the existence (I am not a big fan of applied mathematics, but just the existence is useless for applications, and people in combinatorics never hesitated to stress that combinatorics is very important for applications.
Of course, if one is unable to construct something, it may be very reassuring to know that this something exists. So, such theorems have a legitimate and respectable place.
The very basic applications of the probabilistic method (such as the famous lower bound on diagonal Ramsey numbers) fit the pure-counting pattern you mention, and of course you can equally well write these arguments as counting arguments without bringing probability in.
DeleteBut almost everything proved via the probabilistic method does not reduce to counting structures, but rather weighted structures. The idea is still the same, if the weights of A and B combined is less than one then there is a structure without either A or B, that this works was obvious 9,999 years ago. The point is that one has a reasonable way of choosing these weights (a bad choice will not work, as if you put too much weight on A intersect B then the sum will get bigger than one even though there are events outside A union B) and a lot of tools from probability theory which let one work with these weights. Of course one can always get rid of the probability and just do weighted counting, but it rapidly gets unmanageably complex, unintuitive and you need to prove counting inequalities for yourself that correspond to standard bounds in probability theory (e.g. Azuma-Hoeffding, dependent variables coupled to independent variables bounded using Chernoff, et cetera).
For people who really care about applications, the probabilistic method is (usually, not always) good: to get the desired object, just follow the random procedure, and the desired object is produced with high probability (This is not always true, but algorithmic versions of some of the cases where it looks false have been proved recently). If you are scared you might be unlucky, either you can verify the desired properties quickly (often true) and repeat your random experiment till you verifiably succeed, or you can generally make your failure probability on the order of 10^{-30} (often it's exponentially small, so this is not hard) at which point you can really stop worrying - this latter is often used in practice.
Dear Pete,
DeleteIt is never an issue if some abstract theory can be replaced by "elementary" arguments. First, you always can unravel the abstract definitions and get a proof on a lower level. Then you remove everything not related to your theorem, and you may get a shorter proof in the end. There are also some genuinely elementary proofs, like the proof of the Prime Number Theorem by Selberg (sometimes attributed to Erdös, or to both of them). People were searching for such a proof for decades. But it turned out to be useless, compared with the complex analysis proof.
I don’t quite understand that you are trying to say next. Of course, you can count with weights; this was known long before the probabilistic methods. Definitely, the proofs will be more complicated, and ready to use probabilistic language may simplify your work. Or may not: it depends on your education. Personally, I prefer to avoid the probabilistic language if possible. The probability theory is a very mysterious theory for an outsider. Its modern formalization hardly related to our intuitive notion of probability; it is not natural mathematically (even some leading experts admit this). But this is a completely different topic.
You argument about applications shows, in my view, that the probabilistic method should be augmented by a new idea in order to be applied. Namely, as you described: try any random objects, check if it is good enough, if not, repeat. This is a simple idea, but, probably, is something like a conceptual advance. But it is not part of the probabilistic method. Large prime numbers (which have a commercial value now!) are produced in this way, for example.
Dear Sowa,
ReplyDeleteLet me say a few words in defense of the probabilistic method. I met applications of the probabilistic method when it is not applied to prove that an object satisfying certain properties exists but to estimate a cardinality of a collection of objects that satisfy certain properties. In such cases, we do not consider the objects being counted as random, then "count" them (a 10,000 year old idea, as you said). Instead, some new randomness is introduced. For example, to count surfaces we throw random points in the ambient space and then we count by averaging and, perhaps, using constraints on the volume between the surfaces. Nontrivial modern concentration of measure results generally play an important role. In this form, the idea is probably not older than I am. Personally, when I first encountered such arguments I did not think I could have easily come up with it myself. In a way, this is a radical new way of thinking.
Dear Tamas Gabal,
ReplyDeleteThere is no real need to “defend” the probabilistic method. My claim is not that it is some junk, but that it is what the term “probabilistic method” means. Namely, it is a method, and not a new concept. It is a technique useful for proving some theorems. I tried to study it at least two times from books considered as the best (the first one is, probably, not considered as the best anymore, but it was the only one accessible to me at the time). Both attempts were rather disappointing.
I feel quite differently about the concentration of the measure. I am inclined to consider the discovery of this phenomenon as a conceptual advance, although, to the best of my knowledge, it did not took yet the form of a new definition. Before the very this moment I never thought about why I consider it a conceptual advance. I believe that I do not have to revise my understanding of what is conceptual. Rather, we should wait some time and the definitions will emerge themselves. The concentration of the measure phenomenon is not known as widely as it deserves. I witnessed a talk about it at which quite broadly knowledgeable analysts were present, and the first example of the concentration of the measure was a sort of shock for them. One of them was, apparently, smarter than others (although others were much more renowned as analysts than he), suggested the right way to comprehend the concentration of the measure. Namely, to use a little bit of multidimensional calculus.
I don’t know about which results are you talking (I would be thankful for references), but it seems to me that you are talking not about the probabilistic method, but about something much deeper.
Dear Sowa,
ReplyDeleteI was talking about the results in the Geometry chapter of "The Probabilistic Method" by Alon and Spencer. Other applications of nontrivial concentration inequalities are included in some other chapters as well. Unfortunately, this does not mean that I recommend this book to those who just want to expand their mathematical knowledge. In my opinion, the style of writing is terrible (although, the reviewers on amazon seem to think otherwise) and I rarely used it myself. It is a pity how few book by mathematicians are well written. Is it the pressure to advance their career, publishing papers, obtaining grants, etc., that even good mathematicians put so little effort into passing their knowledge by writing good books?
Well, I believe that Alon-Spencer has that status of the best book in the field, or at least had it several years ago. This is one of the books I attempted to read. The reviews at Amazon describe the book correctly. The number of stars does not matter. They like such book, I don't. Everything is in an agreement: the status of the authors and of their book, Amazon reviews, my own experience with this book, my opinion that the probabilistic method is not a conceptual advance. The reviews say that the book consists of a lot of interesting examples of applications of the probabilistic method, i.e. of the simple idea I stated above. I think that a collection of examples is not an exposition of a conceptual theory. Perhaps, it is not even an exposition of any theory at all.
ReplyDeleteThere are many very well written mathematical books, but certainly not enough of them. Many areas of mathematics are not exposed in any good book. In fact, some areas did not get into any book at all. There are many reasons for this. Let me name just a couple of them (may be I will write about this in some details later). First, to be a good writer and to be a good mathematician is independent qualities. One can write decently without any special writer gift, but one needs to be taught how to write mathematical texts. This is almost never done. Second, expository work is not rewarded in the modern academia, at least in mathematics. If one is interested in how and how long she or he will be remembered, then writing expository texts is essential (as once wrote G.-C. Rota). But people think more about the current salaries, invited talks, etc.
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?
ReplyDeleteDear Tamas Gabal,
ReplyDeleteI tried to answer your question in the next post New ideas.
There is a hierarchy of things a mathematician can do
ReplyDelete(1) A computation
(2) A proof
(3) A useful definition
It is (3) which is the most difficult and the people who don't get the point just don't have the experience.
Unknown:
ReplyDeleteAbout right, except it is not clear what do you mean by a "computation".
A computation in a proper sense is not mathematics. At the same time mathematicians often use it in a very wide sense, like in "computing the homotopy groups of spheres" – such things may involve very deep proofs and may require new definitions. In this sense "to compute" means almost "to find an answer" to a question.