Did J. Lurie solved any big problem?

Previous post: Guessing who will get Fields medals - Some history and 2014.

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.

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

Previous post: About Timothy Gowers.

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.


Next post: New comments to the post "What is mathematics?"

About Timothy Gowers

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

This post was started as a reply to a comment by vznvzn. It had quickly overgrown the comment format, but still is mostly a reply to vznvzn's remarks.

Gowers did not identify any “new mathematical strand/style”, and did not even attempt this. The opposition “conceptual” mathematics vs. “Hungarian” combinatorics was well known for quite a long time. It started to be associated with Hungary only after P. Erdös started to promote an extreme version of this style; but it was known for centuries. When I was in high school, it was known to any student attending a school with teaching of mathematics and physics on a fairly advanced level and having some interest in mathematics. Of course, this is not about UK (Gowers is a British mathematician). I don’t know enough about the schools there.

There is nothing new in looking at the big picture and doing what you called “mathematical anthropology” either. It is just an accident that you encountered such things in Gowers’s two essays first. I doubt that you are familiar with his writing style in mathematics, and even in more technical parts of his essay “Rough Structure and Classification” (by the way, it is available not only as a .ps file; I have a .pdf file in my computer and a hard copy). Gowers’s writing style and his mathematics are very left-brained. I saw no evidence that he even understands how right-brained mathematicians are working. Apparently he does not like the results of their thinking (but carefully tries to hide this in his popular writings). This may be the main reason why he believes that computers can do mathematics. It seems to me that his post-1998 kind of mathematics (I am not familiar enough with his work on Banach spaces, for which he was awarded Fields medal) indeed can be automated. If CS people do need this, then, please, go ahead. This will eliminate this kind of activities from mathematics without endangering the existence of mathematics or influencing its core.

But when Gowers writes some plain English prose, he is excellent. Note that the verbal communication is associated with the left half of the brain.

The left-right brain theory is not such a clear-cut dichotomy as it initially was. But I like it not so much as a scientific theory, but as a useful metaphor. Apparently, you are right and these days most of mathematicians are left-brained. But this is an artifact of the current system of education in Western countries and not an inherent property of mathematics. Almost all mathematics taught in schools and in undergraduate classes of universities is left-brained. This bias reaches its top during the first two years of undergraduate education, when students are required to take the calculus courses (and very often there are no other options). Only the left-brained aspect of calculus is taught in the US universities. Students are trained to perform some standard algorithms (a task which can be done now, probably, even by a smart phone). The calculus taught is the left-brained Leibniz’s calculus, while the right-brained Newton’s calculus is ignored. So, right-brained people are very likely not to choose mathematics as a career: their experience tells them that this is a very alien to them activity.

In fact, a mathematician usually needs both halves of the brain. Some people flourish using only the left half – if their abilities are very high. Others flourish using only right half. But the right half flourishing is only for geniuses, more or less. With all abilities concentrated in the right half, a mathematician is usually unable to write papers in a readable manner. If the results are extremely interesting, other will voluntarily take the job of reconstructing proofs and writing them down. (It would be much better if such work was rewarded in some tangible sense.) Otherwise, there will be no publications, and hence no jobs. The person is out of profession. On a middle level one can survive mostly on the left half by writing a huge amount of insignificant papers (the barrier to “huge” is much lower in mathematics than in other sciences). Similar effects were observed in special experiments involving middle school students. Right-brained perform better in mathematics in general, but if one considers only mathematically gifted students, both halves are equally developed.

What you consider as Gowers’s “project/program of analysis of different schools of thought” is not due to Gowers. This is done by mathematicians all the time, and some of them wrote very insightful papers and even books about this. His two essays are actually a very interesting material for thinking about “different schools”; they provide an invaluable insight into thinking of a partisan of only one very narrow school.

You are wrong in believing that history of mathematics has very long cycles. Definitely, not cycles, but let us keep this word. Mathematics of 1960 was radically different from mathematics of 1950. I personally observed two hardly predictable changes.

There is no “paradigm shift identified” by Gowers. Apparently, Kuhn's concept of paradigm shift does not apply to mathematics at all. The basic assumptions of mathematics had never changed, only refined.

There is another notion of a “shift”, namely, Wigner’s shift of the second kind. It happens when scientists lose interest in some class of problems and move to a different area. This is exactly what Gowers tries to accomplish: to shift the focus of mathematical research from conceptual (right-brained) one to the one that needs only pure “executive power” (left-brained, the term belongs to G. Hardy) at the lowest level of abstraction. If he succeeds, the transfer of mathematics from humans to computers will be, probably, possible. But it will be another “mathematics”. Our current mathematics is a human activity, involving tastes, emotions, a sense of beauty, etc. If it is not done by humans and especially if the proofs are not readable by humans (as is the case with all computer-assisted proofs of something non-trivial to date), it is not mathematics. The value for the humanity of theorems about arithmetic progressions is zero if they are proved by computers. It is near zero anyhow.

Here all three main directions of Gowers’s activities merge: the promotion of combinatorics; the attempt to eliminate human mathematics; his drive for influence and power.

Thanks for appreciating my comments as “visionary”, no matter of that kind. But they are not. What I was doing in my comments to two Gowers’s posts and in this blog is just pointing out some facts, which are, unfortunately, unknown to Gowers’s admirers, especially to the young ones or experts in other fields. Hardly anything mentioned is new; recent events are all documented on the web. I intentionally refrain from using ideas which may be interpreted as my own – they would be dismissed on this ground alone.

I agree that the discussion in Gowers’s blog eventually turned out to be interesting. But only after the people who demanded me to identify myself and asked why I allow myself to criticize Gowers have left. Then several real mathematicians showed up, and the discussion immediately started to make sense. I hope that the discussion in Gowers’s blog was useful at least for some people. The same about this blog. Right now it shows up as 7^th entry in Google search on “t gowers mathematics” (the 2^nd entry is Wiki; other five at the top are his own blogs, pages, etc.) It will go down, of course: I have no intention to devote all my life to an analysis of his mathematics and his personality. And, hopefully, he will eventually cease to attract such an interest as now.

In any case, at least one person definitely benefitted from all this – myself. These discussions helped me to clarify my own views and ideas.

Next post: What is combinatorics and what this blog is about according to Igor Pak.

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?

Next post: About Timothy Gowers.

The conceptual mathematics vs. the classical (combinatorial) one.

Previous post: Simons's video protection, youtube.com, etc.

This post is an attempt to answer some questions of ACM in a form not requiring knowledge of Grothendieck ideas or anything simlilar.

But it is self-contained and touches upon important and hardly wide known issues.

--------------------------------------------

It is not easy to explain how conceptual theorems and proofs, especially the ones of the level close to the one of Grothendieck work, could be at the same time more easy and more difficult at the same time. In fact, they are easy in one sense and difficult in another. The conceptual mathematics depends on – what one expect here? – on new concepts, or, what is the same, on the new definitions in order to solve new problems. The hard part is to discover appropriate definitions. After this proofs are very natural and straightforward up to being completely trivial in many situations. They are easy. Classically, the convoluted proofs with artificial tricks were valued most of all. Classically, it is desirable to have a most elementary proof possible, no matter how complicated it is.

A lot of efforts were devoted to attempts to prove the theorem about the distribution of primes elementary. In this case the requirement was not to use the theory of complex functions. Finally, such proof was found, and it turned out to be useless. Neither the first elementary proof, nor subsequent ones had clarified anything, and none helped to prove a much more precise form of this theorem, known as Riemann hypothesis (this is still an open problem which many consider as the most important problem in mathematics).

Let me try to do this using a simple example, which, perhaps, I had already mentioned (I am sure that I spoke about it quite recently, but it may be not online). This example is not a “model” or a toy, it is real.

Probably, you know about the so-called Fundamental Theorem of Calculus, usually wrongly attributed to Newton and Leibniz (it was known earlier, and, for example, was presented in the lectures and a textbook of Newton's teacher, John Barrow). It relates the derivatives with integrals. Nothing useful can be done without it. Now, one can integrate not only functions of real numbers, but also functions of two variables (having two real numbers as the input), three, and so on. One can also differentiate functions of several variables (basically, by considering them only along straight lines and using the usual derivatives). A function of, say, 5 variables has 5 derivatives, called its partial derivatives.

Now, the natural question to ask is if there is an analogue of the Fundamental Theorem of Calculus for functions of several variables. In 19^th century such analogues were needed for applications. Then 3 theorems of this sort were proved, namely, the theorems of Gauss-Ostrogradsky (they discovered it independently of each other, and I am not sure if there was a third such mathematician or not), Green, and Stokes (some people, as far as I remember, attribute it to J.C. Maxwell, but it is called the Stokes theorem anyhow). The Gauss-Ostrogradsky theorem deals with integration over 3-dimensional domains in space, the Green theorem with 2 dimensional planar domains, and the Stokes theorem deals with integration over curved surfaces in the usual 3-dimensional space. I hope that I did not mix them up; the reason why this could happen is at the heart of the matter. Of course, I can check this in moment; but then an important point would be less transparent.

Here are 3 theorems, clearly dealing with similar phenomena, but looking very differently and having different and not quite obvious proofs. But there are useful functions of more than 3 variables. What about them? There is a gap in my knowledge of the history of mathematics: I don’t know any named theorem dealing with more variables, except the final one. Apparently, nobody wrote even a moderately detailed history of the intermediate period between the 3 theorems above and the final version.

The final version is called the Stokes theorem again, despite Stokes has nothing do with it (except that he proved that special case). It applies to functions of any number of variables and even to functions defined on so-called smooth manifolds, the higher-dimensional generalization of surfaces. On manifolds, variables can be introduced only locally, near any point; and manifolds themselves are not assumed to be contained in some nice ambient space like the Euclidean space. So, the final version is much more general. And the final version has exactly the same form in all dimension, but the above mentioned 3 theorems are its immediate corollaries. This is why it is so easy to forget which names are associated to which particular case.

And – surprise! – the proof of general Stokes theorem is trivial. There is a nice short (but very dense) book “Calculus on manifolds” by M. Spivak devoted to this theorem.  I recommend reading its preface to anybody interested in one way or another in mathematics. For mathematicians to know its content is a must. In the preface M. Spivak explains what happened. All the proofs are now trivial because all the difficulties were transferred into definitions. In fact, this Stokes theorem deals with integration not of functions, but of the so-called differential form, sometimes called also exterior forms. And this is a difficult notion. It requires very deep insights to discover it, and it still difficult to learn it. In the simplest situation, where nothing depends on any variables, it was discovered by H. Grassmann in the middle of 19^th century. The discoveries of this German school teacher are so important that the American Mathematical Society published an English translation of one of his books few years ago. It is still quite a mystery how he arrived at his definitions. With the benefits of hindsight, one may say that he was working on geometric problems, but was guided by the abstract algebra (which did not exist till 1930). Later on his ideas were generalized in order to allow everything to depend on some variables (probably, E. Cartan was the main contributor here). In 1930ies the general Stokes theorem was well known to experts. Nowadays, it is possible to teach it to bright undergraduates in any decent US university, but there are not enough of such bright undergraduates. It should be in some of the required course for graduate students, but one can get a Ph.D. without being ever exposed to it.

To sum up, the modern Stokes theorem requires learning a new and not very well motivated (apparently, even the Grassmann did not really understood why he introduced his exterior forms) notion of differential forms and their basic properties. Then you have a theorem from which all 19^th century results follow immediately, and which is infinitely more general than all of them together. At the same time it has the same form for any number of variables and has a trivial proof (and the proofs of the needed theorems about differential forms are also trivial). There are no tricks in the proofs; they are very natural and straightforward. All difficulties were moved into definitions.

Now, what is hard and what is difficult? New definitions of such importance are infinitely rarer than new theorems. Most mathematicians of even the highest caliber did not discover any such definition. Only a minority of Abel prize winner discovered anything comparable, and it is still too early to judge if their definitions are really important. So, discovering new concepts is hard and rare. Then there is a common prejudice against anything new (I am amazed that it took more than 15 years to convince public to buy HD TV sets, despite they are better in the most obvious sense), and there is a real difficulties in learning these new notions. For example, there is a notion of a derived category (it comes from the Grothendieck school), which most of mathematicians consider as difficult and hardly relevant. All proofs in this theory are utterly trivial.

Final note: the new conceptual proofs are often longer than the classical proofs even of the same results. This is because in the classical mathematics various tricks leading to shortcut through an argument are highly valued, and anything artificial is not valued at all in the conceptual mathematics.

Next post: The Hungarian Combinatorics from an Advanced Standpoint.

Reply to Timothy Gowers

Previous post: Happy New Year!


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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