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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).

Next post: Reply to JSE.

## About the title

**About the title**

I changed the title of the blog on March 20, 2013 (it used to have the title “Notes of an owl”). This was my immediate reaction to the news the T. Gowers was presenting to the public the works of P. Deligne on the occasion of the award of the Abel prize to Deligne in 2013 (by his own admission, T. Gowers is not qualified to do this).

The issue at hand is not just the lack of qualification; the real issue is that the award to P. Deligne is, unfortunately, the best compensation to the mathematical community for the 2012 award of Abel prize to Szemerédi. I predicted Deligne before the announcement on these grounds alone. I would prefer if the prize to P. Deligne would be awarded out of pure appreciation of his work.I believe that mathematicians urgently need to stop the growth of Gowers's influence, and, first of all, his initiatives in mathematical publishing. I wrote extensively about the first one; now there is another: to take over the arXiv overlay electronic journals. The same arguments apply.

Now it looks like this title is very good, contrary to my initial opinion. And there is no way back.

## Sunday, March 24, 2013

### Reply to Timothy Gowers

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