Geometry and Theory

John Baez's latest offering is up, and once again has a mindboggling mouthful of mathematical magic.

I liked this section:

...this reminds me of something Feynman wrote: whenever he worked on a problem, he needed the feeling he had some "inside track" - some insight or trick up his sleeve that nobody else had. Most of us will never be as good as Feynman at choosing an "inside track". But I think we all need one to convert what would otherwise be a dutiful and doomed struggle to catch up with the experts into something more hopeful and exciting: a personal quest!

...

For anyone with a background in geometry, a good "inside track" on almost any math problem is to convert it into a geometry problem.

If you read nothing else in his post, read the last section, containing a beautiful quotation from Alain Connes. This is an excerpt:

The really fundamental point in that respect is that while so many mathematicians have been spending their entire life exploring that world they all agree on its contours and on its connexity: whatever the origin of one's itinerary, one day or another if one walks long enough, one is bound to reach a well known town i.e. for instance to meet elliptic functions, modular forms, zeta functions. "All roads lead to Rome" and the mathematical world is "connected".

In other words there is just "one" mathematical world, whose exploration is the task of all mathematicians, and they are all in the same boat somehow

Which brings me to a topic that Jeff brings up: Is computational geometry still part of the theoryCS landscape ? Jeff's answer is spot-on, if a little tongue-in-cheek: Of course it is !! But he is also right that reality seems to suggest otherwise. Lance and Sariel (and Jeff, again) push the discussion further, and interesting points are made in the comments on all blogs. These points are tactical, in that they discuss the logistics of large meetings, the "too specialized for STOC/FOCS" phenomenon, and other ways of increasing socialization.

But really, if you want to have geometry (or any other sub-area of theory) be viewed as central within the larger landscape, tactical methods are not what does it. Ultimately, a practising researcher has to ask themselves, "What does knowing more about the tools and techniques in this area give me" ? And most researchers instinctively focus on areas and topics that affect their work in a day-to-day sense. This is not to say that one remains specialized (and balkanized), it's that the way people move from area to area is by natural drifts from their current choice of problem, rather than by teleportation.

Which brings me back to the picturesque 'landscape' of Alaine Connes. What valuable exports does computational geometry currently have to offer to the travelling theoretician ? There is a rich structure of tools and techniques in computational geometry, and an unparalleled array of methods for working in polynomial time (something that work in approximations, for example, tends to give short shrift to). Any story of the power of randomization has to contain large doses of geometry, for this is where its power has been exploited most successfully.

But not many of the techniques familiar to most geometers are extended (or extensible in the current world) to problems that lie squarely in theory land, but outside the realm of geometry. The best (and only example) I can think of is how Mulmuley uses the Collins decomposition and other tools from algebraic geometry in his P vs NC result. Machine learning of course makes heavy use of VC-dimension methods, but geometers can't really claim ownership of this idea either, though we have used it extensively.

I will admit that the point I make is extreme, and is deliberately so. But I am merely trying to argue that if I work in (say) graph approximations, I am unlikely to need to know methods or results from computational geometry beyond what is directly needed for a problem I am working on. Thus, any interest I will have in geometry will be purely from a general sense of curiosity about the area. In these specialized times, this is really not enough to keep me abreast of the latest results and methods in the field.

I use the word 'current', and the present tense, because I don't believe that this situation will continue indefinitely. Fields evolve and change, and we are still in the early days of exploring the theoryCS landscape. Furthermore, CG is not the only 'isolated city'; other areas face the same problem, and until brave souls take a machete to the thickets and forge roads between these cities, we will continue to bemoan the lack of attention our pet subfield gets in the overall scheme of things.

So here's a challenge: let CG be the 'inside track' that Baez speaks of. Let's see if we can find problems that need a "geometric approach" to break a logjam or prove a new result. Do this even once or twice, and the interest in the field will grow, naturally.

But what in the meantime ? One of my more radical beliefs is a conviction that the 'conference-as-main-pub' model is not working for us any more, primarily for reasons of scale. Further, the growth of areas in theory is making the whole STOC/FOCS idea of a central 'theory conference' less and less a model of reality. I liked the suggestion on Lance's blog that we should have an FTRC for theory areas; after all, this would be very similar to the omnibus conferences that are common in the math world.

This post has become far too long, so I'll stop here :).