The n-Category Café

Maybe I’d need a clear crisp summary to see what motivates your interest here.

Ok. So I’d like a clearer sense of answers to:

How are the interests of current mathematical researchers distributed within the space of mathematics? What is the connectivity of this distribution? How is the distribution evolving? How ought it to evolve? What are the internal goods of mathematics?

Gowers in his essay is pointing out that his area of research makes little connection with the monumental constructions of algebraic geometry, algebraic number theory, etc., but that people make the further mistake of imagining his ‘combinatorics’ to involve a sequence of unconnected problems, whose solution requires one-off triumphs of ingenuity. He gives Ramsey theory as an example:

Theorem. For every positive integer $k$ there is a positive integer $N$, such that if the edges of the complete graph on $N$ vertices are all coloured either red or blue, then there must be $k$ vertices such that all edges joining them have the same colour. The least integer $N$ that works is known as $R(k)$.

Problem. (i) Does there exist a constant $a \gt \sqrt{2}$ such that $R(k) \ge a^k$ for all sufficiently large $k$. (ii) Does there exist a constant $b \lt 4$ such that $R(k) \le b^k$ for all sufficiently large $k$?

I consider this to be one of the major problems in combinatorics and have devoted many months of my life unsuccessfully trying to solve it. And yet I feel almost embarrassed to write this, conscious as I am that many mathematicians would regard the question as more of a puzzle than a serious mathematical problem.

Odd isn’t it that a Fields’ medallist needs to defend himself like this? But he must have heard the charge. Google Books is cutting it off, but we get the gist from this statement by Saunders Mac Lane

There are also all manner of small problems, some natural, some concocted, problems are a vehicle of competition and display. In some schools (often in those influenced by Hungarian traditions) the business of mathematics seems to be just the formulation and the eventual solution of hard problems, with perhaps more attention to the difficulty than to the… (Mathematics: Form and Function, 430)

Gowers defends his interest by observing that any breakthrough in Ramsey theory is likely to involve a new general principle of potential broad significance to combinatorics, but that this new principle will most probably not be expressible as general theory. If so, this suggests that not all general principles may be expressed as what you call, following Lawvere, the general abstract.

So there are questions of how best to characterise the space of existing mathematical research, e.g., is it just to be expected that some parts won’t connect? I presume that you’re not going to be listening out intently to find out whether someone has shaved some epsilon off the bounds of the Ramsey number, whereas, you might want to hear of someone in $p$-adic Langlands couch their work in a way that makes you see what $p$-adic cohesiveness must be. But, as Elkies and Tao suggest, maybe there are useful bridges to be build between more combinatorial or analytic areas and the grand theories. If so, will we need to find a common characterisation? What if the best way to characterise the structure of the ‘combinatorics’ part of mathematics is not category-theoretic?

And then there are questions of value. Beyond something being valued because it relates to your interests, do you think pieces of research have value in terms of the good of mathematics itself? Do you think anyone should care about lengths of arithmetic progressions in random subsets of the integers? How do you feel about

Theorem. For every $\delta \gt 0$ there exists $N$ such that every subset of ${1, 2,...,N}$ of size at least $\delta N$ (that is, density at least $\delta$) contains an arithmetic progression of length three?

What could make such a result more valuable? If it tied in with a “noisy additive cohomology”?

I presume that you’re not going to be listening out intently to find out whether someone has shaved some epsilon off the bounds of the Ramsey number,

I might well be – if I knew, or as soon as I know, that it is part of the answer to a question that I care about.

Lest the impression is falsely gotten between the lines of our discussion that I spend my life just doing general abstract math, maybe let me remind you (you all) that I have a physics degree, have a good bit of my publications in mathematical physics, and am quite used to spending days with chasing signs, and integrands and the like. Sometimes I think that because I was brought up in an academic world bare of any general abstract, I came to appreciate it more than others who take it for granted. I had to fight for it, nobody around me appreciated it when I was a student. And I had several revelations where mountains of concrete particular tedious work collapsed and disappeared because finally the right general abstract perspective was found.

When I learned string theory, like any other student, I was exposed to the anecdote of Jacobi’s abstruse identity which is maybe a good illustration for our discussion.

Jacobi in 1892 figured out that the following is true:

$$\frac{1}{2 \sqrt{x}} \left( \prod_{n=1}^{\infty} \left( \frac{1 + x^{n-1/2}}{1-x^n} \right)^8 - \prod_{n=1}^\infty \left( \frac{1- x^{n-1/2}}{1-x^n} \right)^8 \right) = 8 \prod_{n=1}^\infty \left( \frac{1+x^n}{1-x^n} \right)^8 \,.$$

This is abstruse, isn’t it? About as abstruse as Ramsey theory, maybe. Jacobi proved it – god knows how and why – it didn’t mean anything to anybody, and he moved on to prove other things… until a century later suddenly it turns out that it is the truth of this identity that makes superstring theory tick. And suddenly it is clear what it is this weird equation is actually saying: it counts the number of bosonic and of fermionic states of the superstring, and asserts that they are equal. This is exceptional.

And in more than one sense. In fact there is a long list of similar (if maybe not quite as impressive) very non-general-abstract exceptional identities in all kinds of fields of math whose truth turns out to be the reason for the supersymmetry of some QFT in some dimension. Supersymmetry is a major source of exceptional structures in math. I am in principle interested in each and every one of these – number of hours in the day being the limiting factor.

Gowers defends his interest by observing that any breakthrough in Ramsey theory is likely to involve a new general principle of potential broad significance to combinatorics, but that this new principle will most probably not be expressible as general theory. If so, this suggests that not all general principles may be expressed as what you call, following Lawvere, the general abstract.

This paragraph I do not quite understand. I should probably read Gowers’ orginal. I find already the distinction between “a general principle of broad significance” and a “general theory” subtle, and much more so if both of these together with this distinction is now conjectured. This makes me think that I can’t really know what this discussion is about.

you might want to hear of someone in p-adic Langlands couch their work in a way that makes you see what $p$-adic cohesiveness must be.

You know, I am not that interested in cohesiveness in itself. I will probably not spend a whole lot of energy in understanding whatever random model of cohesion somebody suggests. I am interested in cohesion as a means to an end. It so happens that it turns out to be a major machine that helps me whith what I am really interested in: understanding physics. And it helps me distinguish which parts of physics are general abstract, which are exceptional. For instance we learned from cohesive $\infty$-topos theory that the structure of Chern-Simons theory and its higher dimensional siblings is hard-wired at the very, very foundation of mathematical structure, much more fundamental even than the fundamental role it plays in physics really suggests. This changed my perspective on these action functionals. At the same time, we are busy tabulating the exceptional structures found here: while the structure of $\infty$-Chern-Simons theory is fundamental general abstract, every single one of them comes from some cocycle, and these oranize, as usual, as various infinite series with plenty of exceptional instances. All of them most interesting to study, no general nonsense explaining their properties.

maybe there are useful bridges to be build between more combinatorial or analytic areas and the grand theories.

Beyond something being valued because it relates to your interests, do you think pieces of research have value in terms of the good of mathematics itself?

I am not sure I see how anyone can value mathematics beyond it relating to his or her interest. Would I say: here is a completely uninteresting piece of mathematics, but I value it because it meets the following abstract criteria? These criteria will be imposed because they are interesting to somebody for some reason.

Mathematics is all about being intersted in something, isn’t it?

Do you think anyone should care about lengths of arithmetic progressions in random subsets of the integers?

I am glad that somebody cares about it, so that the moment I discover why I need it, there is somebody who already knows about it!

I am every second day discovering some remote piece of math that I never knew what it was good for and suddenly I see how it springs out of, say, cohesive topos theory. Then I am glad that somebody already worked it all out. Parts of my writing of the “cohesive document” was work along these lines: “Look, this fits here, and this fits here, and this fits here.”

Does the story of Jacobi’s abstruse identity tell us anything more than that an apparently obscure result can become important? The lesson is that we need to be careful in our assessment of value because connections may be forged in the future to other pieces of theory. But it doesn’t tell us about what is a worthy thing to forge to (other than that being a central result for string theory is good) or how this forging takes place, and these are the topics of Gowers’ essay.

Let’s leave aside the contentious value topic altogether, since it’s the topic of Brendan’s second conference, and think about differences of method. What is the glue that holds what Gowers calls ‘combinatorics’ together? You say you should probably read Gowers’ original essay, which is certainly true, but if you only have a couple of minutes and want to know what interests me in it, here is an extract.

He writes,

In general, as one gains experience at solving problems in an area such as combinatorics, one finds that certain difficulties recur. It may not be possible to express these difficulties in the form of a precisely stated conjecture, so instead one often focuses on a particular problem which involves those difficulties. The problem then takes on an importance which goes beyond merely finding out whether the answer to it is yes or no. This explains why it was possible for so many of Erdos’s problems to have hidden depths.

Then

It is perhaps helpful to consider various different ways that one branch of mathematics can be of benet to another. Here is a list, in order of directness (but not exhaustive), of how area A can help area B.
(i) A theorem of A has an immediate and useful consequence in B.
(ii) A theorem of A has a consequence in B, but it takes some work to prove it.
(iii) A theorem of A resembles a question in B sufficiently closely to enable one to imitate or adapt the A-proof and answer the B-question.
(iv) In order to solve a problem in A, one is led to develop tools in B which are of independent interest.
(v) Area B contains definitions which resemble those of area A. (To give just one example, sometimes one wishes to define a notion of independence which behaves in some but not all ways like linear independence in vector spaces.) Area A then suggests fruitful ways of organizing and tackling the results and problems in B.
(vi) If one gains an expertise in area A, then one picks up certain habits of thought which enable one to make a significant contribution to area B.
(vii) Area A is sufficiently close in spirit to area B, that anybody who is good at area A is likely to be good at area B. Moreover, many mathematicians make contributions to both areas.

So, I find that an interesting thought that whatever allows for that transfer of skill from A to B, especially towards the end of the list, is difficult to formulate explicitly. When I first read the essay, I felt myself doubt the possibility that there could be no general formulation explaining such connections, that it was a matter of time before a general theory emerged. But who is to say? Then what kinds of general formulations are possible? Are there non-category-theoretic frameworks for such general formulations?

To make any progress on these, we would have to look at concrete examples, perhaps taking Gowers’ own lead:

As for (vi) and (vii), I can speak from personal experience, having worked recently on several problems outside Banach space theory. Although I have not applied Banach-space results, my experience in that area has enabled me to think about problems in ways that would not otherwise have occurred to me. And I am far from alone in this, as many mathematicians who have worked on Banach spaces have worked successfully in other areas as well, such as harmonic analysis, partial differential equations, C*-algebras, probability and combinatorics.

Incidently, when calling for cross-cultural work towards the end of the essay, Gowers writes

collaboration of this kind would require greater efforts on the part of problem-solvers to learn a bit of theory, and greater sympathy on the part of theoreticians towards mathematicians who do not know what cohomology is.

Interesting how cohomology is taken to represent the other side.

I see that Gowers says explicitly that his list is not exhaustive, but all the same I’m quite surprised not to see anything along the lines of “the definitions of area A provide a useful organizing principle for definitions and theorems in area B”. That seems to be very often the role played by A=category theory.

I felt myself doubt the possibility that there could be no general formulation explaining such connections, that it was a matter of time before a general theory emerged. But who is to say?

An excellent point. I would guess that I probably speak for many when I say that one of the things that first attracted me to category theory was that it does provide a general formulation of such connections. If I think back (with an effort) to a time before I had heard the word “category”, I think it was not at all obvious to me that relationships of this form could ever be formalized precisely. That’s why it was such a revelation to me to realize that there was a formal definition which included both groups and group homomorphisms, rings and ring homomorphisms, modules and module homomorphisms, etc.

One might say that what mathematics does is to see connections between different things and make them precise in a general theory by rising to a higher level of abstraction, and so it’s only natural that this activity could act upon itself as well. But there’s even less reason to expect that all relationships outside mathematics can be formalized mathematically, so why should it be the case inside mathematics? Maybe this is a case of “unreasonable effectiveness” leading us to mistakenly expect universal effectiveness.

Does the story of Jacobi’s abstruse identity tell us anything more than that an apparently obscure result can become important?

Yes, it does, I think. Whether it’s “important” that the superstring is consistent is something easily debateable and debated. The point here is rather: the abstruse identity turns out to be a concrete particular of a (more) general abstract: namely of supersymmetry representation theory.

The lesson is that we need to be careful in our assessment of value because connections may be forged in the future to other pieces of theory.

I thought of a different lesson. Getting back to the point I raised at the beginning: I am still wondering if the “two cultures” are not simply the two fields of study that every mathematician must necessarily be both interested in, that of the general abstract and of its concrete models.

Studying representation theory of super Lie algebras is something very much towards the general abstract end of the pattern. But every single instance it considers may be very peculiar. So what at Jacobi’s times may have seemed to be a quasi-random result is now understood to be of interest as a model for a nice structured theory. So if I am interested in the general abstract of susy representation theory, I will necessarily also be interest in various abstruse identities that may seem to be from a “different culture”. But they are not.

Thanks, yes. My fingers must have been thinking of ring spectra when they typed this.