The news of Ian Agols claimed proof of the Virtually Haken/fibered conjectures is very exciting and I look forward to reading Danny Calegari’s summaries of Ian’s talks. But at the same time, I remember the time after Perelmann announced his proof of the Poincare conjecture and the dire predictions of the end of 3-manifold topology, and I wonder what the aftermath will be this time.

The most visible aspect of this subject has always been its open problems – The Poincare conjecture at first, then Thurston’s suite of problems, including the VHC. Many (most? all?) fields are guided by major open problems, but 3-dimensional topology stands out for borrowing most of its most powerful techniques from outside – algebra, geometry, dynamical systems, gauge theory, etc. These connections have invigorated and popularized the field, but they have also created a situation in which when a major problem falls, so does the field’s public image.

Every field goes through cycles in which an innovation changes the landscape, the new ideas are explored, refined and consolidated, then the field quiets down while waiting for the next innovation. I hope and expect that the proof of the VHC will be the beginning of a phase of exploration and consolidation, rather than the beginning of dormancy.

In the long term, of course, it’s much harder to say. There are still plenty of open questions in 3-dimensional topology, though none as visible as Thurston’s conjectures. I’ve mentioned WYSIWYG geometry/topology in past posts, though this has not yet coalesced into a single major open problem worthy of the attention that Thurston’s conjectures received. There are plenty of other directions as well that I am unqualified to write about.

But it’s interesting that the proofs of the major conjectures that drove topology research for 100 years come at the same time as real world applications of topology are suddenly appearing. You may have read about knot theory being used to understand the dynamics of DNA, but there are also problems emerging related to understanding the structure of large data sets. These days, a science experiment may produce results consisting of hundreds or thousands of points in a vector space with hundreds or thousands of dimensions. Organizing this data into a form that can be understood by a human requires a great deal of topological understanding. On the other hand, most of the techniques that have been developed so far are topologically rather naive. While there may be no direct connection to 3-dimensional topology, I would claim that the intuition and ideas that come from dealing with with abstract 3-dimensional spaces can be extremely valuable for understanding these problems. (I will give more specific evidence for this in upcoming posts.)

I believe that applying ideas from low dimensional topology to problems in data analysis has the potential to not only create more outside interest in the field, but also to enrich the field by suggesting new directions to explore. In my next few posts, I plan to describe some of the types of problems that arise in understanding large data sets, describe the ways that ideas from different areas of topology have already been used to attack these problems, and discuss/speculate on how ideas from low dimensional topology could be used in the future.

There are still huge open problems in low-dimensional topology, problems that are maybe not quite as well-cultured as Thurston’s problems but huge open problems nonetheless, like the smooth 4-dimensional Poincare Conjecture, the 4-dimensional Schoenflies problem, the world of knot and 3-manifold concordance is still very fruitful, there are some big open problems related to the Vassiliev spectral sequence, spaces of knots, and other spaces-of-stuff/borderline continuum mechanics type problems (rope length, etc), the big world of relations to mathematics inspired by physics. There’s also plenty of “housekeeping” problems, lesser-known open problems that have been neglected that people will realize they can tackle now, and of course, there’s lots of very productive mathematics people could do by revising and perhaps simplifying the mass of techniques known nowadays as “3-manifold theory”.

But as you say, the entire subject of topology, not just low-dimensional topology has reached a level of maturity where people inside and outside the field are more keen on applying the subject to other areas. I think that will be one of the most productive outgrowths in the near future. I’m currently working with an engineer applying Carlsson’s techniques to certain types of data. The engineer (an old friend) was curious to see what kinds of insights these techniques could bring, so it’s a fun project to analyze data he’s very familiar with, to see if these methods will see anything other more traditional methods from stats do not see.

Comment by Ryan Budney — March 30, 2012 @ 3:05 pm |

Good, I’m glad other low dimensional topologists feel the same way as I do!

Comment by Jesse Johnson — March 30, 2012 @ 4:19 pm |

On that subject, one of my personal pet Future Visions right now is the need to start flowing back from applied algebraic topology into pure mathematics. I’m pretty active in Gunnar Carlsson’s style of topological data analysis, and often find myself wanting to pull the technique of persistent homology back into combinatorics or geometry.

Comment by michiexile — March 31, 2012 @ 12:06 am

Well… it would be interesting to see if the following two problems are now doable

1 Are 3-manifold groups linear?

2. Is the simple loop conjecture true for 3-manifolds?

More intriguing would be progress on the Galewski-Stern triangulation obstruction problem of finding (if it exists) a homology 3-sphere such that its connected sum with itself bounds an acyclic 4-manifold.

As far as applications, I will point out that geometric topology is not unique in its status as a very cool (in my opinion) subject in search of a “good” application. Holograms have been around in quantity since the 60’s but are still in search of a “good” application. For geometric topology, I would suggest, only partly tongue in cheek, creating some really cool computer games and calling it a day.

Comment by Mayer A. Landau — March 30, 2012 @ 7:54 pm |

The Agol–Wise developments represent major progress on the question of linearity. Liu proved that non-positively curved graph manifolds are virtually (non-compact) special, which implies that they are -linear (cf. the work of Przytycki and Wise). There is active work on extending these results to all non-positively curved 3-manifolds; this would reduce the question of linearity to certain graph manifold groups.

The simple loop conjecture is another matter. It’s false for limit groups, which Wise proved are virtually special. So it’s hard to see how the work of Wise and Agol helps in this direction.

Comment by Henry Wilton — April 2, 2012 @ 4:34 am |

@Mayer, I wouldn’t characterize this discussion as one of people looking for a “good” application, as there are already good applications. If we were to personalize this more, it’s about what happens to a goal-driven person once they’ve achieved their goals. Thurston’s conjectures were major landmarks people used to gauge the significance of their own and others’ work in the field. The conjectures provided a context for people to work in. So there’s a desire now to broaden the context and ask ourselves, “okay what should the new benchmarks be? How will we perceive success in the future?” Algebraic topology passed a similar threshold perhaps sometime in the 70’s after the h-cobordism theorem was proven and many of the major “reduce everything to problems about the homotopy groups of spheres” theories were set up. The field has been less dominated by concrete problems and agreed-upon agendas since.

Comment by Ryan Budney — March 31, 2012 @ 3:26 am |

Hi Ryan. I agree with Danny Calegari’s comment that “this is the end of an era in 3-manifold topology”, with Jesse Johnson’s comment that 3-manifold topology currently lacks problems that are “as visible as Thurston’s conjectures”, and with your comment that the field currently lacks conjectures that provide “a context for people to work in”. Perhaps (who knows?) future work will suffer due to a lack of “agreed-upon agenda”. Because of this, I imagine that right now 3-manifold topologists are in a celebratory frame of mind, tempered perhaps with a little nostalgia for yonder years when the subject was more of a frontier field. But …, I am of the opinion that it should be all celebration and no nostalgia for the following two reasons. First, it’s not like the field is over. There will always be an infinite area to explore. Second, the fact that a broad, concrete rubric or map is now constructed for 3-manifold topology, creates an enormous teaching opportunity. 3-manifold topology is uniquely suited for exposing students to the unifying aspects of mathematics, as it borrows from so many different parts of mathematics – as pointed out by Jesse Johnson above. And, 3-manifold topology opens a whole vista on geometry that a high school or beginning undergraduate could never have imagined. I think by exposing students to 3-manifold topology, they cannot help but be drawn in by the sheer wonder of it all. If you take a step back, the whole framework is rather mind-boggling.

Comment by Mayer A. Landau — March 31, 2012 @ 6:11 pm |

Thank for this post- I think we had all been thinking this. The same way there were 3-Dimensional Topology after Perelman conferences (whose title is a bit dismissive of Perelman’s chances to return to 3-dimensional topology, I feel), we’re surely now going to be thinking about the face of “3-dimensional topology after VHC”.

First, in the immediate future, we have a decent chance of generating positive publicity for our field with this development. I’ve been reading “Why a 100-year old difficult problem was solved”, a popular book in Japanese about Perelman and Geometrization, which has Perelman figuring out the shape of the universe. It sold pretty well to the non-mathematical public, and is better than any other pop-science account of the affair that I know. I think mathematics can be publicized and advertised even more powerfully this time around, bringing more funding and drawing more young people in. UC Berkeley where Ian Agol works, for example, surely needs the funding. One might sell the story as “3-dimensional shapes classified!”. That would be the hype.

Regarding the actual state of 3-manifold topology, it seems to me that its most basic problem, the Classification Problem for 3-manifolds, is still wide open.

I think that in fact 3-manifolds have been classified on only an extremely weak sense- right now, to identify a 3-manifold, we need to know its decomposition into finite-volume geometric submanifolds (algorithmically painful), then we need to know all finite covers of each of the hyperbolic pieces (even more algorithmically painful- indeed, impossible if the word “all” is to be taken literally), and finally we need to tabulate surface bundles over the circle (exponential-time algorithm). If somebody were to hand you a 3-manifold, how long would it take you to classify it? If the bound on algorithm running-time were ridiculous, in what sense could you claim to have classified 3-manifolds?

The current situation is reminiscent the situation in knot theory half a century ago. In 1962, Haken classified knots in some weak sense- Hemion completed this approach in 1979. The effect on knot theory was quite minor, because the algorithm was impractical.

So “Classify 3-manifolds” [in polynomial time] still seems to me to be the big open problem in 3-dimensional topology.

By the way, what is the situation for 3-manifolds with boundary? (or faces?). How can we try to classify them?

Beyond all of that, 4-manifold topology is a complete mystery- Slice-Ribbon is a major important difficult conjecture, not to mention the Smooth 4-D Poincare Conjecture and related problems. The structure of the knot concordance group seems completely mysterious.

Quantum topology is another complete mystery, where 30 years on we still can’t answer the simplest most-naive questions, such as “What is the topological meaning of the Jones polynomial?”. The Volume Conjecture and related problems are also wide open, and quite hard; and their eventual solutions will surely have to involve substantial new useful ideas.

Comment by dmoskovich — March 31, 2012 @ 8:12 pm |

[...] Here are also few relevant posts from the blog: Low dimensional topology. A post about Wise conjecture (that Agol proved) with references and links; An earlier post on Wise’s work; A post VHC post; [...]

Pingback by Exciting News on Three Dimensional Manifolds | Combinatorics and more — April 1, 2012 @ 2:15 pm |

I think, generally speaking, great progress leads to more great progress, and witnessing it now after Perelmann makes it more reassuring.

Comment by Gil Kalai — April 2, 2012 @ 4:06 am |

[...] After the VHC (It is an interesting paradox that a field can become LESS exciting when an open problem in that field is solved) [...]

Pingback by Fifteenth Linkfest — April 2, 2012 @ 9:18 am |

One great problem (that perhaps Ian Agol already solved but I am not sure what the status is) is if triviality of knots is in coNP.

Comment by Gil Kalai — April 4, 2012 @ 2:16 am |

There has been some very recent progress on whether knot triviality is in coNP. Greg Kuperberg has established this, with the assumption of the Generalized Riemann Hypothesis. This marks the first application of the GRH in knot theory, to my knowledge. The result is posted on the arxives.

Comment by Joel Hass — April 5, 2012 @ 2:12 am |

Dear Joel, remarkable! many thanks

Comment by Gil Kalai — April 8, 2012 @ 4:45 am

[...] In fact, one of my professors from undergraduate, Jesse Johnson, wrote a nice little blog post on what it might mean for the future of low dimensional topology. Basically, Agol used this special cube complex stuff [...]

Pingback by So tubular! Err… cubular « Baking and Math — December 10, 2012 @ 11:27 am |