Open Problems

First, I want to give a quick advertisement for a Floer homology open problem website run by John Baldwin (https://floerhomologyproblems.blogspot.com/).  This has a mix of problems, some of which seem very hard, and some of which might be a bit more manageable.  If I was more thoughtful, I would collect a bunch of different open problem lists here for reference, but I'm not that thoughtful. 

Speaking of which, if you're a younger grad student or someone adjacent but not in low-dimensional topology, you may not be familiar with the famous Kirby problem list from the 1990s.  (That is an update of an initial list made by Kirby many years earlier.)  Many of these problems have been solved (e.g. the 3D Poincare Conjecture), but many of the outstanding ones are the biggest problems in the field (e.g. the 4D Smooth Poincare Conjecture, additivity of unknotting number under connected sum, etc) and have guided a lot of research directions.  If you solve a Kirby problem, it definitely adds to your brand (which is important for getting invited to give talks, jobs, etc).   

I want to make several comments on the Kirby problem list:

- While some of the problems are very big and difficult and have withstood the probing of all known methods, many problems are still just waiting for the right application of the correct new idea/invariant/etc.  I think it's good to be familiar with some Kirby problems you find interesting and spend a little time working on them.  Even if you don't have the idea or the tool, you can learn a lot from the previous approaches, etc.  You can also keep coming back to them as you learn more and more and eventually you will find the right tool to solve it!  (Sometimes you even had the tools all along, and should have done it many years earlier...)  It has certainly directed a lot of my research throughout the years. 

- There are two updates to the Kirby problem list that are forthcoming eventually, being led by Inanc Baykur, Rob Kirby, and Danny Ruberman.  The first is an update on the status of all the problems in the list (many have been solved!).  The second is a new problem list, which includes some problems from the previous list and several other problems to be added.  I'm hopeful both of these will appear within the next year or two, and that it will invigorate the field with a lot of new excitement.  

- It feels strange not to point out that there's definitely controversy around Kirby as a mathematician for the views he has expressed on sexism in mathematics (see, e.g. this very old article or this more recent article on the new list).  While I disagree with his views, I think that the problem list has and will continue to play a crucial role in directing the field.  Last fall there was a gathering of low-dimensional topologists to work on the new list, and it was pointed out to me that perhaps many people decided not to come because of his involvement in it.  As a result, I'm curious as to whether that might in turn shape what problems/subfields are represented in the new list.      

- Either as a symptom of or cause for the problem list, this field has become fairly problem-solving focused.  It's the gold standard to solve a Kirby problem, and if you can't do that, you try to solve a special case or another open problem from a paper/list or something of the sort.  As a result, it's not clear to me that the field puts as much value in general theory building as in say symplectic geometry.  Concretely, I wonder if it would be valuable to have an open problem list that focused more on general theory building in the area.  

 - This all leads me to ask some general questions about open problems.  What is the right thing for any field to be most focused on?  Should we be solving these types of problems which the field is deeply interested in (e.g. the smooth Poincare conjecture) or would it be better if we were more proactive about trying to direct the field towards connections with other fields or scientific disciplines that might benefit from our work?  Are the problems we're solving the most important low-dimensional topics for mathematics or science in general?  Should we be focused more long term on building more tools which might be useful later in our field and possibly in other fields way down the line, or dreaming up pipe dreams for how to really transform the field?  For example, perhaps proposing a novel strategy for classifying smooth structures on 4-manifolds which does not yet have good evidence is more valuable than finding another exotic smooth structure on some generic 4-manifold.  Another question is whether we should really broaden the scope of the field?  As a different example, a ton of people in the field have worked on unknotting numbers; but almost no one in our field is thinking about physical knots (knots with some thickness) even though there's still lots of open questions about these too and are perhaps more relevant to the real world.  Why such an imbalance?  If we think a problem is important, why do we just have 50 people working in parallel on some of the same problems?  Wouldn't it make more sense to decide as a field that we want to solve a specific problem and create a larger community approach to solving it?  (AIM workshops are some kind of attempt at this, but it's not really that structured of an approach.)  To be honest, sometimes I feel that I continue to do variations of what I already know because that's what I know I can do; as a result, I don't step back and think think about what the true purpose of the field should be.  I think we should all be doing this.  In addition to developing open problems lists (and solving them!), I think there should be more discussions around these broader questions in the community.