What is combinatorics and what this blog is about according to Igor Pak

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I came across the post “What is Combinatorics?” by Igor Pak. His intention seems to be refuting what is, in his opinion, a basic fault of my notes, namely, the lack of understanding of what is combinatorics.

“While myself uninterested in engaging in conversation, I figured that there got to be some old “war-time” replies which I can show to the Owl blogger.  As I see it, only the lack of knowledge can explain these nearsighted generalizations the blogger is showing.  And in the age of Google Scholar, there really is no excuse for not knowing the history of the subject, and its traditional sensitivities.”

Unfortunately, he did not show me anything. I come across his post while searching other things by Google. May be he is afraid that giving me a link in a comment will engage him in conversation? I would be glad to discuss these issues with him, but if he is not inclined, how can I insist? My intention was to write a comment in his blog, but for this one needs to be registered at WordPress.com. Google is more generous, as is T. Gowers, who allows non-WordPress comments in his blog.

Indeed, I don't know much about “traditional sensitivities” of combinatorics. A Google search resulted in links to his post and to numerous papers about “noise sensitivity”.

Beyond this, he is fighting windmills. I agree with most of what he wrote. Gian-Carlo Rota is my hero also. But I devoted a lot of time and space to explaining what I mean by "combinatorial" mathematics, and even stated that I use this term only because it is used by Gowers (and all my writings on this topics have a root in his ones), and I wasn't able to find quickly a good replacement (any suggestions?). See, for example, the beginning of the post “The conceptual mathematics vs. the classical (combinatorial) one” , as also other posts and my comments in Gowers's blog. In particular, I said that there is no real division between Gowers's “second culture” and “first culture”, and therefore there is no real division between combbinatorics and non-combinatorics.

So, for this blog the working definition of combinatorics is “branches of mathematics described in two essays by T. Gowers as belonging to the second culture and opposed in spirit to the Grothendieck's mathematics”.

I don't like much boxing of all theorems or papers into various classes, be they invented by AMS, NSF, or other “authorities”. I cannot say what is my branch of mathematics. Administrators usually assign to me the field my Ph.D. thesis belongs to, but I did not worked in it since then. I believe that the usual division of mathematics into Analysis, Algebra, Combinatorics, Geometry, etc. is hopelessly outdated.


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The Hungarian Combinatorics from an Advanced Standpoint

Previous post: Conceptual mathematics vs. the classical (combinatorial) one.

Again,  this post is a long reply to questions posed by ACM. It is a complement to the previous post "Conceptual mathematics vs. the classical (combinatorial) one". The title is intentionally similar to the titles of three well known books by F. Klein.

First, the terminology in “Conceptual mathematics vs. the classical (combinatorial) one” is my and was invented at the spot, and the word "classical" is a very bad choice. I should find something better. The word "conceptual" is good enough, but not as catchy as I may like. I meant something real, but as close as possible to the Gowers's idea of "two cultures". I do not believe in his theory anymore; but by simply using his terms I will promote it.

Another choice, regularly used in discussions in Gowers's blog is "combinatorial". It looks like it immediately leads to confusion, as one may see from your question (but not only). First of all (I already mentioned it in Gowers's blog or here), there two rather different types of combinatorics. At one pole there is the algebraic combinatorics and most of the enumerative combinatorics. R. Stanley and the late J.-C. Rota are among the best (or the best) in this field. One can give even a more extreme example, mentioned by M. Emerton: symmetric group and its representations. Partitions of natural numbers are at the core of this theory, and in this sense it is combinatorics. One the other hand, it was always considered as a part of the theory of representations, a highly conceptual branch of mathematics.

So, there is already a lot of conceptual and quite interesting combinatorics. And the same time, there is Hungarian combinatorics, best represented by the Hungarian school. It is usually associated with P. Erdös and since the last year Abel prize is also firmly associated with E. Szemerédi. Currently T. Gowers is its primary spokesperson, with T. Tao serving as supposedly independent and objective supporter. Of course, all this goes back for centuries.

Today the most obvious difference between these two kinds of combinatorics is the fact that the algebraic combinatorics is mostly about exact values and identities, and Hungarian combinatorics is mostly about estimates and asymptotics. If no reasonable estimate is in sight, the existence is good enough. This is the case with the original version of Szemerédi's theorem. T. Gowers added to it some estimates, which are huge but a least could be written down by elementary means. He also proved that any estimate should be huge (in a precise sense). I think that the short paper proving the latter (probably, it was Gowers's first publication in the field) is the most important result around Szemerédi’s theorem. It is strange that it got almost no publicity, especially if compared with his other papers and Green-Tao's ones. It could be the case that this opinion results from the influence of a classmate, who used to stress that lower estimates are much more deep and important than the upper ones (for positive numbers, of course), especially in combinatorial problems.

Indeed, I do consider Hungarian combinatorics as the opposite of all new conceptual ideas discovered during the last 100 years. This, obviously, does not mean that the results of Hungarian combinatorics cannot be approached conceptually. We have an example at hand: Furstenberg’s proof of Szemerédi theorem. It seems that it was obtained within a year of the publication of Szemerédi’s theorem (did not checked right now). Of course, I cannot exclude the possibility that Furstenberg worked on this problem (or his framework for his proof without having this particular application as the main goal) for years within his usual conceptual framework, and missed by only few months. I wonder how mathematics would look now if Furstenberg would be the first to solve the problem.

One cannot approach the area (not the results alone) of Hungarian combinatorics from any conceptual point of view, since the Hungarian combinatorics is not conceptual almost by the definition (definitely by its description by Gowers in his “Two cultures”). I adhere to the motto “Proofs are more important than theorems, definitions are more important than proofs”. In fact, I was adhering to it long before I learned about this phrase; this was my taste already in the middle school (I should confess that I realized this only recently). Of course, I should apply it uniformly. In particular, the Hungarian style of proofs (very convoluted combinations of well known pieces, as a first approximation) is more essential than the results proved, and the insistence on being elementary but difficult should be taken very seriously – it excludes any deep definitions.

I am not aware of any case when “heuristic” of Hungarian combinatorics lead anybody to conceptual results. The theorems can (again, Furstenberg), but they are not heuristics.

I am not in the business of predicting the future, but I see only two ways for Hungarian combinatorics, assuming that the conceptual mathematics is not abandoned. Note that still not even ideas of Grothendieck are completely explored, and, according to his coauthor J. Dieudonne, there are enough ideas in Grothendieck’s work to occupy mathematicians for centuries to come – the conceptual mathematics has no internal reasons to die in any foreseeable future. Either the Hungarian combinatorics will mature by itself and will develop new concepts which eventually will turn it into a part of conceptual mathematics. There are at least germs of such development. For example, matroids (discovered by H. Whitney, one of the greatest topologists of the 20^th century) are only at the next level of abstraction after the graphs, but matroids is an immensely useful notion (unfortunately, it is hardly taught anywhere, which severely impedes its uses). Or it will remain a collection of elementary tricks, and will resemble more and more the collection of mathematical Olympiads problems. Then it will die out and forgotten.

I doubt that any area of mathematics, which failed to conceptualize in a reasonable time, survived as an active area of research. Note that the meaning of the word “reasonable” changes with time itself; at the very least because of the huge variations of the number of working mathematicians during the history. Any suggestions of counterexamples?

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Reply to Timothy Gowers

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Here is a reply to a comment by T. Gowers about my post My affair with Szemerédi-Gowers mathematics.

I agree that we have no way to know what will happen with combinatorics or any other branch of mathematics. From my point of view, your “intermediate possibility” (namely, developing some artificial way of conceptualization) does not qualify as a way to make it “conceptual” (actually, a proper conceptualization cannot be artificial essentially by the definition) and is not an attractive perspective at all. By the way, the use of algebraic geometry as a reference point in this discussion is purely accidental. A lot of other branches of mathematics are conceptual, and in every branch there are more conceptual and less conceptual subbranches. As is well known, even Deligne’s completion of proof of Weil’s conjectures was not conceptual enough for Grothendick.

Let me clarify how I understand the term “conceptual”. A theory is conceptual if most of the difficulties were moved from proofs to definitions (i.e. to concepts), or they are there from the very beginning (which may happen only inside of an already conceptual theory). The definitions may be difficult to digest at the first encounter, but the proofs are straightforward. A very good and elementary example is provided by the modern form of the Stokes theorem. In 19th century we had the fundamental theorem of calculus and 3 theorems, respectively due to Gauss-Ostrogradsky, Green, and Stokes, dealing with more complicated integrals. Now we have only one theorem, usually called Stokes theorem, valid for all dimensions. After all definitions are put in place, its proof is trivial. M. Spivak nicely explains this in the preface to his classics, “Calculus on manifolds”. (I would like to note in parentheses that if the algebraic concepts are chosen more carefully than in his book, then the whole theory would be noticeably simpler and the definitions would be easier to digest. Unfortunately, such approaches did not found their way into the textbooks yet.) So, in this case the conceptualization leads to trivial proofs and much more general results. Moreover, its opens the way to further developments: the de Rham cohomology turns into the most natural next thing to study.

I think that for every branch of mathematics and every theory such a conceptualization eventually turns into a necessity: without it the subject grows into a huge body of interrelated and cross-referenced results and eventually falls apart into many to a big extent isolated problems. I even suspect that your desire to have a sort of at least semi-intelligent version of MathSciNet (if I remember correctly, you wrote about this in your GAFA 2000 paper) was largely motivated by the difficulty to work in such a field.

This naturally leads us to one more scenario (the 3rd one, if we lump together your “intermediate” scenario with the failure to develop a conceptual framework) for a not conceptualized theory: it will die slowly. This happens from time to time: a lot of branches of analysis which flourished at the beginning of 20th century are forgotten by now. There is even a recent example involving a quintessentially conceptual part of mathematics and the first Abel prize winner, J.-P. Serre. As H. Weyl stressed in his address to 1954 Congress, the Fields medal was awarded to Serre for his spectacular work (his thesis) on spectral sequences and their applications to the homotopy groups, especially to the homotopy groups of spheres (the problem of computing these groups was at the center of attention of leading topologists for about 15 years without any serious successes). Serre did not push his method to its limits; he already started to move to first complex manifolds, then algebraic geometry, and eventually to the algebraic number theory. Others did, and this quickly resulted in a highly chaotic collection of computations with the Leray-Serre spectral sequences plus some elementary consideration. Assuming the main properties of these spectral sequences (which can be used without any real understanding of spectral sequences), the theory lacked any conceptual framework. Serre lost interest even in the results, not just in proofs. This theory is long dead. The surviving part is based on further conceptual developments: the Adams spectral sequence, then the Adams-Novikov spectral sequence. This line of development is alive and well till now.

Another example of a dead theory is the Euclid geometry.

In view of all this, it seems that there are only the following options for a mathematical theory or a branch of mathematics: to continuously develop proper conceptualizations or to die and have its results relegated to the books for gifted students (undergraduate students in the modern US, high school students in some other places and times).


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