### Articulating your program

- a range of new algebraic structures, with new applications and new results in traditional areas;
- new viewpoints on classical material;
- better understanding, from a higher dimensional viewpoint, of some phenomena in group theory;
- new computations with these objects, and hence also in the areas in which they apply;
- new algebraic understanding of the structure of certain geometric situations;
- a stimulus to new ideas in related areas;
- a range of unexplored ideas and potential applications;
- the solution of some classical famous problems.

...just as Poincaré’s conjecture, [The Geometrization Conjecture] is likely not to be resolved quickly, but I hope it will be a more productive guide to research on 3-manifolds than Poincaré’s question has proven to be. (p. 358)‘Three Dimensional Manifolds, Kleinian Groups and Hyperbolic Geometry’, Bulletin of the American Mathematical Society 6: 357-81. It is possible that after Perelman's work he may have chosen to reassess his opinion.

Elsewhere in algebraic topology, Mark Hovey has a page of problems which he hopes will help steer algebraic topology in useful directions:

Before proceeding onto the problems, I want to make a few polemical remarks about algebraic topology. The field is a small one, and to some extent we have been marginalized in mathematics. This is completely ridiculous, since the methods and ideas of algebraic topology have broad application to other areas of mathematics--witness Voevosdky's recent Fields Medal caliber work. We as algebraic topologists must bear part of the responsibility for this marginalization, and we must attempt to improve the situation. There are two ways we can do this. The most obvious method is to work on problems that arise externally to algebraic topology but for which the methods of algebraic topology may be helpful. This is a tough situation to get into--I don't think I have ever managed it--but very much worth it. Much of the action in mathematics in the last 10 years has come from interactions with physics, and algebraic topology can probably say more than it has. See any recent paper of Jack Morava for some ideas on this score.From his major problems page:However, even if the problems we work on are internal to algebraic topology, we must strive to express ourselves better. If we expect our papers to be accepted in mathematical journals with a wide audience, such as the Annals, JAMS, or the Inventiones, then we must make sure our introductions are readable by generic good mathematicians. I always think of the French, myself--I want Serre to be able to understand what my paper is about. Another idea is to think of your advisor's advisor, who was probably trained 40 or 50 years ago. Make sure your advisor's advisor can understand your introduction. Another point of view comes from Mike Hopkins, who told me that we must tell a story in the introduction. Don't jump right into the middle of it with "Let E be an E-infinity ring spectrum". That does not help our field.

The biggest problem, in my opinion, is to come up with a specific vision of where homotopy theory should go, analogous to the Weil conjectures in algebraic geometry or the Ravenel conjectures in our field in the late 70s. You can't win the Fields Medal without a Fields Medal-winning problem; Deligne would not be DELIGNE without the Weil conjectures and Mike Hopkins would not be MIKE HOPKINS without the Ravenel conjectures. We can't all be Deligne or Mike, but making the conjectures requires different talents than proving them, and more of us might have a chance. This was actually my motivation for making this list; to provide a forum for conjectures so that we might collectively be able to form a program analogous to the Weil conjectures. This would make a huge difference to our field, I think. Of course, they have to be somewhat accessible conjectures, which the problems below may not be!Moving to physics, Michael Nielsen includes his post on Narratives and the justification of science amongst his favourites.

String theory, astrophysics, and (to a lesser extent) condensed matter and AMO [atomic, molecular and optical] physics have all done a terrific job of articulatingLike Hovey, he's worried that his field, quantum information theory, hasn't promoted itself sufficiently. A lesson to both might be that devoting considerable resources to this activity may not be enough. While the future of higher-dimensional algebra seems assured, the future of Brown's pioneering department in Bangor is less certain.whythey matter. They’ve identified deep central questions that are relatively timeless and unarguably important. Furthermore, they’ve communicated those questions clearly and repeatedly, not just within physics, but to other scientists, and, in some instances, to the public at large.

Update: For a very clear account about what category theory is good for see Brown and Porter's contribution to What is Category Theory? (Polimetrica, forthcoming). It's called 'Category Theory: an abstract setting for analogy and comparison'.

## 1 Comments:

David writes:

What one must be ready to do, if one follows this line of reasoning, is to demote a famous problem if it turns out not to be a good indicator in this way. Even about the Poincaré conjecture, William Thurston could say this:

...just as Poincaré’s conjecture, [The Geometrization Conjecture] is likely not to be resolved quickly, but I hope it will be a more productive guide to research on 3-manifolds than Poincaré’s question has proven to be. (p. 358)

‘Three Dimensional Manifolds, Kleinian Groups and Hyperbolic Geometry’, Bulletin of the American Mathematical Society 6: 357-81. It is possible that after Perelman's work he may have chosen to reassess his opinion.

I doubt it. Thurston's geometrization conjecture has the Poincaré conjecture as a corollary. Perelman's work is devoted to proving Thurston's geometrization conjecture and getting the Poincaré conjecture as a corollary. So, I think Thurston's opinion above will be

confirmedby Perelman's apparent success.Nobody came close to proving the Poincaré conjecture until it was seen to be a spinoff of Thurston's

bigger, more ambitious but more conceptual and thus more interesting problem. This is a standard pattern in mathematics: bite off more, so there's more to chew on!For example, nobody had come close to proving Fermat's last theorem until it was seen (by Frey) to be a spinoff of the Taniyama-Shimura conjecture, which is now a theorem thanks to Wiles, Breuil, Conrad, Diamond and Taylor.

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