13 June, 2009

updated September 17, 2014

On the category theory discussion list, a question was asked about `famous problems in category theory'-- see the end of this comment. Here is a slightly revised version of my response. This prompted a lot of discussion which can be found on the archives.

I remember being asked this kind of question at a Topology conference in Baku in 1987. It is worth discussing the background to this, as someone who has never gone for a `famous problem', but found myself trying to develop some mathematics to express some basic intuitions.

Stanislaw Ulam remarked to me in 1964 at my first international conference (Syracuse, Sicily) that a young person may feel the most ambitious thing to do is to tackle a famous problem; but this may distract that person from developing the mathematics most appropriate to them. It was interesting that this remark came from someone as good as Ulam!

G.-C. Rota writes in `Indiscrete thoughts' (1997):

What can you prove with exterior algebra that you cannot prove without it?" Whenever you hear this question raised about some new piece of mathematics, be assured that you are likely to be in the presence of something important. In my time, I have heard it repeated for random variables, Laurent Schwartz' theory of distributions, ideles and Grothendieck's schemes, to mention only a few. A proper retort might be: "You are right. There is nothing in yesterday's mathematics that could not also be proved without it. Exterior algebra is not meant to prove old facts, it is meant to disclose a new world. Disclosing new worlds is as worthwhile a mathematical enterprise as proving old conjectures. "

It is like the old military question: do you make a frontal attack; or find a way of rendering the obstacle obsolete?

I was early seduced (see my first two papers in my publication list ) by the idea of looking for questions satisfying 3 criteria:

1) no-one had previously asked it;

2) the question was technically easy to answer;

3) the answer was important.

Usually it has been 2) which failed!

Of course you do not find such questions where everyone is looking! See the streetlight effect

It could
be interesting to investigate how such questions arise, perhaps by pushing
a point of view as far as it will go, or seeing a new analogy. In my case the questions discussed in my first two papers, what we now see as that of
cartesian and monoidal closed categories of topological spaces,
came at the end of writing the rest of my DPhil thesis, and arose from consideration of that work.

"If at first, the idea is not absurd, then there is no hope for it." Albert Einstein.

It could be interesting to investigate the following historically:

if (let us suppose) category theory has advanced without a fund of famous open problems, how then has it advanced?

One aim of mathematics is understanding, making difficult things easy, seeing why something is true. Thus improved exposition is an important part of the progress of mathematics (even if this is ignored by Research Assessment Exercises). R. Bott said to me (1958) that Grothendieck was prepared to work very hard to make something tautological. By contrast, a famous algebraic topologist replied to a question of mine about his graduate text by asking: `Is the function not continuous?' He never gave me a proof! And I never found it! (Actually the function was not well defined, but that I could fix!)

Grothendieck wrote to me in 1982: `The introduction of the cipher 0 or the group concept was general nonsense too, and mathematics was more or less stagnating for thousands of years because nobody was around to take such childish steps ...'. See also

The point I am trying to make is that the question on `open problems' raises issues on the nature of, on professionalism in, and so on the methodology of, mathematics. It is a good question to start with.

Hope that helps.

Ronnie Brown

On further thought, one might relate an emphasis on famous problems to ideas of `thought control', in an Orwellian sense. I have noticed since the 1970s a tendency among some top people (even or perhaps especially FRS's?) to use words like `rubbish, nonsense, ridiculous' to describe new ideas, but often when pressed they are unable or unwilling to elaborate on these terms, even when they are used to describe a mathematical theory with carefully written definitions, examples, theorems, proofs, and so on. This poverty of language is a kind of newspeak, in Orwell's sense, and is possibly connected with the idea of power. It might also be connected with a prescriptive educational system in mathematics which values examination performance on given tasks above independence and creativity, and the discussion of the aims, context and successes of mathematics. See also the discussion on Promoting Mathematics.

If a succession of `top people' suggest that what one has pursued to the best of one's professional capabilities is `rubbish, nonsense, ridiculous', then this raises the stakes!

I confess to being not so interested in other peoples' problems. My work on higher dimensional group theory was motivated by the idea of developing some mathematics to express some intuitions which would enable a proof. It is good fun to develop a mathematical theory almost from scratch.

Others have said that it is harder to ask a good question than to answer an already formulated question! As noted in The methodology of mathematics, a 1974 report on mathematicians in employment stated that they were `good at problem solving, not so good at problem formulation'.

There is a kind of tyranny about associating the progress of mathematics with the solution of famous problems. Of course it is easy to give a formal assessment of someone's achievement in the solution of such a problem: one can grade a mathematician in this type of work as one can grade a tennis player on his or her success. What is much more difficult, maybe even impossible, is to grade the potential of new ideas. See Einstein's quote above. Also :"Whoever undertakes to set himself up as a judge of Truth and Knowledge is shipwrecked by the laughter of the gods." (Albert Einstein) ((Actually, I learn from the internet that the quote is from Edmund Burke's Preface to Brissot's Address (1794)!)

Further, the public and other scientists are not necessarily interested in these `famous problems' which are often incomprehensible to that potential audience. I have found that these audiences are interested in new concepts, if only one can explain them to these audiences, and like to know that mathematics is developing new outlooks on basic ideas such as logic, structures, language. There is a danger of people asking for bread and being given stones, precious stones perhaps. I refer to my papers [130, 136,137,146,150] for examples of what I have tried to do in this direction, and also to the web site on knots.

Ideal Scenarios

A reasonable research strategy is to look for the wildest possible proposition you can think of. Then you ask yourself : what would happen if in the best of all possible worlds this was true? If the prospect does not thrill you, then perhaps you should give up the idea. On the other hand, suppose that if it all worked out well, the prospects would be amazing, then you ask yourself: there must be great difficulties so what are the obstructions to this working well? If obstructions appear, then this will be interesting. If they gradually disappear or are overcome, then that will be even more interesting! Thus this is a `no lose' strategy!

I have applied this over the years to the idea of `higher dimensional group theory', to which all the words `rubbish, nonsense, ridiculous' have been applied!

J. Montesinos once remarked to me that he tells his research students to continue working on things they find easy!

From: "Hasse Riemann" <rafaelb77@hotmail.com>

To: "Category mailing list" <categories@mta.ca>

Sent: Tuesday, June 02, 2009 5:31 PM

Subject: categories: Famous unsolved problems in ordinary category theory

Hello categorists

I don't know what to make of the silence to my question.This is the easiest question Ihave. I can't believe it is so difficult.

It is not like I am asking you to solve the problems.

There must be some important open problems in ordinary category theory. There are plenty of them in the theory of algebras and in representation theory, so there should be more of them in category theory.

Especially if you broaden the boundaries a bit of what ordinary category theory is.

Take for instance:

model categories,

categorical logic,

categorical quantization,

topos theory-locales-sheaves.

But I had originally pure category theory in mind.

Best regards

Rafael Borowiecki

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