## December 28, 2007

### Challenges for the Future

#### Posted by David Corfield

Benjamin Mann of DARPA has constructed a list of 23 challenges for mathematics over the next century.

Whereas Hilbert notes about his 23 problems

I have generally mentioned problems as definite and special as possible, in the opinion that it is just such definite and special problems that attract us the most and from which the most lasting influence is often exerted upon science,

Mann’s challenges are generally open-ended, resembling Hilbert’s sixth problem:

6. Mathematical treatment of the axioms of physics

The investigations on the foundations of geometry suggest the problem: To treat in the same manner, by means of axioms, those physical sciences in which mathematics plays an important part; in the first rank are the theory of probabilities and mechanics.

rather than his thirteenth:

13. Impossibility of the solution of the general equation of the 7-th degree by means of functions of only two arguments.

Some motivation accompanies Mann’s list, but it would be good to see experts write a few paragraphs for each challenge on that inviting parchment background.

Posted at December 28, 2007 10:53 AM UTC

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### Re: Challenges for the Future

For some inimitable Arnoldian exposition on Hilbert’s thirteenth problem see the first pages of the lecture From Hilbert’s Superposition Problem to Dynamical Systems.

Posted by: David Corfield on December 28, 2007 11:12 AM | Permalink | Reply to this

### Re: Challenges for the Future

Do I seriously understand right that this list is being used as the basis for a DARPA grant program (DARPA Mathematical Challenges, BAA 07-68)? I find this shocking, because I think the list of problems is abysmal.

It’s silly to request proposals for “major mathematical breakthroughs” on the Riemann hypothesis, but at least it’s a worthy goal. By contrast, some of the problem statements appear to me to be gibberish. For example, in Problem 7, is there any meaning to the question “As data collection increases can we ‘do more with less’ by finding lower bounds for sensing complexity in systems?” I have no idea why we are trying to do more with less when data collection is increasing, what lower bounds have to do with actually accomplishing anything, or what it means to sense complexity in systems. The problem title (“Occam’s Razor in Many Dimensions”) and second sentence (“This is related to questions about entropy maximization algoriths.”) help only a little in clarifying.

By contrast, Problem 6 (“Computational Duality: Duality in mathematics has been a profound tool for theoretical understanding. Can it be extended to develop principled computational techniques where duality and geometry are the basis for novel algorithms?”) is already solved. Certainly the statement has been achieved, although one could always develop these ideas further.

Many of the other problems are poorly phrased or extremely speculative. I’m seriously offended by the form of this solicitation for proposals. I imagine it won’t be a big problem, since what will end up happening is that proposers add a brief description of why their proposal is relevant to these problems and DARPA funds the same stuff it would have anyway. However, it’s ridiculous. PIs shouldn’t have to try to guess what the program manager is talking about, and the government shouldn’t waste money trying to flesh out the program manager’s wild ideas.

Posted by: Anonymous on December 28, 2007 8:49 PM | Permalink | Reply to this

### Re: Challenges for the Future

My thoughts exactly anonymous.

What i find even more offending, is the “between the lines” comparison of this guy himself to Hilbert in his motivation. Let alone the quoting of Kelvin and Einstein to give weight to this nonsense, (He should have read Baez’s crackpot story)

My only hope is that this gibberish will eventually lead to a decent set of problems, how general they may be, to be tackled by the 21st century mathematicians..

Posted by: ericv on December 28, 2007 11:34 PM | Permalink | Reply to this

### Re: Challenges for the Future

I’m pretty underwhelmed by this list of problems. Some are quite vague; others seem like random stabs in the dark.

For one of the latter sort consider, problem 23. It first urges that we “SETTLE THE SMOOTH POINCARE CONJECTURE IN DIMENSION 4”. That’s a worthy goal: it would be very nice to know if every smooth compact manifold homotopy equivalent to the 4-sphere is not just homeomorphic but diffeomorphic to $S^4$ with its usual smooth structure.

But then, it asks “What are the implications for space-time and cosmology?” It’s not clear there are any such implications. There might be, if the answer uses a lot of gauge theory. But there might not. People used gauge theory to construct exotic smooth structures on $\mathbb{R}^4$, but nobody really knows the possible consequences for physics yet, despite a few vague speculations.

And then, it asks: “And might the answer unlock the secret of ‘dark energy’?” I see no reason to expect it will.

I could write a much better list myself, especially with the help of other mathematicians — starting with the readers of this blog. But, I won’t unless DARPA pays me to.

Posted by: John Baez on December 29, 2007 8:02 AM | Permalink | Reply to this

### Re: Challenges for the Future

If we had to contribute one problem (or maybe two) to a list of 23 along n-category theoretic lines, what might we choose?

Posted by: David Corfield on December 29, 2007 12:12 PM | Permalink | Reply to this

### Re: Challenges for the Future

If I had to contribute one problem along $n$-category theoretic lines, it would probably be

How can we assemble a team of people to help Urs Schreiber work out his ideas and explain them to a large group of mathematicians and physicists as efficiently as possible?

Anyone who reads and halfway understands Urs’ new paper with Sati and Stasheff should realize that this is an obvious winner… especially compared to risky gambles like ‘settling the smooth Poincaré conjecture and using the answer to unlock the secret of dark energy’.

Posted by: John on December 29, 2007 9:08 PM | Permalink | Reply to this

### Re: Challenges for the Future

I don’t suppose there’s much disagreement that mathematics itself has plenty of room for woolly ideas as well as very concrete ones. As for what is most appropriate in a bureaucratic context where a good deal of money is involved, I really don’t know what to think. But one semi-mathematical comment I have concerns:

What is the role of homotopy theory in the classical, geometric, and quantum Langlands program?’

I agree entirely that this a a very flaky question. But you see, I had thought that this was only *my* flaky question!

MK

Posted by: Minhyong Kim on December 30, 2007 11:52 PM | Permalink | Reply to this

### Re: Challenges for the Future

Hmm, that was one of the ones that seemed less flaky to me. Maybe I just don’t know enough about the Langlands program.

Posted by: John Baez on December 31, 2007 12:49 AM | Permalink | Reply to this

### Re: Challenges for the Future

Right. That’s actually what I was trying to say. Spelled out: I understand if some people see the question as strange. But I’ve had similar questions myself in several different forms. (Except for the quantum’ part, whose meaning I don’t understand.) In fact, I really was quite surprised that some one else had had that question seriously enough for it to appear on that kind of a list.

Posted by: Minhyong Kim on December 31, 2007 5:25 AM | Permalink | Reply to this

### Re: Challenges for the Future

Re: Darpa’s challenges for the future

I dislike posting anonymously, but I’m doing so now because I like flame wars even less; and that’s what this discussion seems perilously close to. I’d urge anyone interested to step back and look at this more calmly.

One of Darpa’s charges is to survey matters of scientific and technological interest, with an eye toward gaps and blind spots in the conventional wisdom. It has recently funded research into the geometric Langlands program, which (among other things) turns out to have nontrivial applications in physics, and I believe that program was regarded as highly successful. I would read Mann’s challenges as an invitation for mathematicians, physicists, computer scientists and related workers to look for important mathematical questions which deserve wider attention (and more funding).

Possible connections between the 4D smooth Poincaré conjecture and cosmology seems to me a quite reasonable example of this sort of question.: it’s arguable that the standard Big Bang model, successful as it is, politely disguises the fact that we really don’t understand the boundary conditions in Einstein’s model for gravitation. The Cauchy problem for GR has an enormous literature, but there isn’t much concern there for the uncountably many smooth structures on Euclidean four-space. Smooth h-cobordisms of three-manifolds are not well-understood either. D-brane models for dark energy given serious attention in physics seem to be extremely speculative; this whole area may be an opportunity for mathematicians, physicists, and computer sciences (interested eg in spin foam models) to benefit from talking to each other.

There is limited funding for mathematical research, and I would read these challenges as a serious attempt to widen those possibilities. It might be most constructive if interested researchers who perceive the questions as off the mark (or not!) would respond to them with considered proposals as to how these questions (or, perhaps, better ones) could be approached. I don’t see these proposals as anything more than an attempt to open a door.

Posted by: anonymous on December 29, 2007 3:18 PM | Permalink | Reply to this

### Re: Challenges for the Future

There is limited funding for mathematical research, and I would read these challenges as a serious attempt to widen those possibilities. It might be most constructive if interested researchers who perceive the questions as off the mark (or not!) would respond to them with considered proposals as to how these questions (or, perhaps, better ones) could be approached. I don’t see these proposals as anything more than an attempt to open a door.

Thanks, I was beginning to worry at the negativity. Above suggestions are good. One more: since the questions are regarded by some as too vague, how about refining them?

Posted by: jim stasheff on December 29, 2007 4:41 PM | Permalink | Reply to this

### Re: Challenges for the Future

I don’t see these proposals as anything more than an attempt to open a door.

That would be great if they weren’t part of an actual solicitation for grant applications. If Mann were just brainstorming about interesting problems and trying to get other people thinking as well, then that would be different. It still wouldn’t be a very impressive start, but it would at least get some discussion going. However, when you send out a call for grant applications, you should make sense.

I am convinced this deserves tremendous negativity. Lots of people spend many hours preparing grant applications. At a minimal level, shouldn’t the DARPA program manager take enough time to make sure the list of problems is actully meaningful? Every problem should have a short statement that at least makes the general theme clear together with enough references to provide further details for experts. It’s disgusting that some of the problems appear to be gibberish, and I mean that in the strong sense: not just that they have no meaning to me, but that they have no meaning to anyone. If I asked an undergraduate class to write up problems and someone turned in Problem #7, for example, they would get an F.

As I said above, this will probably turn out OK, since the stupid stuff will get ignored. However, it’s still an insult and embarrassment to the mathematical community as well as a distraction and waste of time. I have no objection to widening the possibilities for funded research, but this is an incompetent way to go about it.

It’s also worrisome because of what it suggests about Mann’s performance as program manager. If I write a grant proposal that takes up one of his pet topics, promises great results and uses lots of buzzwords and vague descriptions, will he be inclined to fund it? I’m worried that the answer is yes, that his standards for clarity and intellectual rigor are on display in the list of problems. DARPA grant applications should be judged by a higher standard.

So the net result is that I’m outraged by this proposal. Why am I complaining here instead of to DARPA?

(1) I certainly will complain to DARPA. I’m writing a longer, more detailed complaint that discusses a number of the listed problems.

(2) I hope to inspire other people to complain as well. Frankly, I think anyone who cares about the availability of research funds or about how the government spends its money should be complaining.

(3) I’m anonymous here (even though I won’t be when I write to DARPA) since I’m being considered for tenure and afraid of being judged by people who think the best way of dealing with an embarrassment is to pretend it isn’t there, or who think the best way to get money out of government agencies is by non-stop flattery of how wonderful their grant programs are. They may even be right in the second case, but I don’t think maximizing the availability of grant money should be our top intellectual priority.

One more: since the questions are regarded by some as too vague, how about refining them?

For some of them, this might be fine (although the vague versions are already written in stone as part of the grant solicitation). For others, refining them would amount to trying to guess what Mann had in mind. I find it hard to figure out, I don’t really care to try since it’s his interpretations that matter for judging grants rather than mine, and in any case I find developing my own ideas to be more interesting than trying to flesh out the wild ramblings of some random DARPA program manager.

I realize my negative tone might put some people off, but I think it is justified by how awful this grant solicitation is. I’ve always been proud of how sensible and principled the process of applying for math grants is, compared to some other areas in which sponsors try to impose their own wacky ideas on applicants. Like everyone else, the NSF sometimes makes the wrong decision, but (certainly at least in math) it never solicits applications to address gibberish problems.

P.S.

It has recently funded research into the geometric Langlands program, …, and I believe that program was regarded as highly successful.

This is a good example of how DARPA should work. Geometric Langlands wasn’t some wacky idea of the program manager’s (like biological quantum field theory), or worse yet gibberish; rather, DARPA identified a valuable area that could use additional funding and funded it.

I have no objections to DARPA posing their own problems, of course, but those problems should make sense and be actually important.

Posted by: Anonymous #1 on December 29, 2007 7:26 PM | Permalink | Reply to this

### Re: Challenges for the Future

I agree with the negativity expressed by our anonymous friend here.

To take an example: I have nothing against settling the smooth Poincaré conjecture and using the answer to unlock the secret of dark energy. If someone thinks they can do it, they should definitely try! If I were working for DARPA, and a grant proposal described a plausible strategy for doing it, I’d definitely want to fund them! — especially since it’s unlikely to have military applications.

(I guess that’s why I’m not working for DARPA.)

But, I think it’s ridiculous for a formal call for grant proposals to include this on the list of topics. Solving the smooth Poincaré conjecture? Okay, maybe. But applying the unknown answer to crack the puzzle of dark energy? This just means people who are experts on topology will need to pad their grant applications with blather about cosmology… and the best blather may get the grant.

Posted by: John Baez on December 29, 2007 9:24 PM | Permalink | Reply to this

### Re: Challenges for the Future

An anonymous visitor to the café wrote:

Possible connections between the 4D smooth Poincaré conjecture and cosmology seems to me a quite reasonable example of this sort of question: it’s arguable that the standard Big Bang model, successful as it is, politely disguises the fact that we really don’t understand the boundary conditions in Einstein’s model for gravitation. The Cauchy problem for GR has an enormous literature, but there isn’t much concern there for the uncountably many smooth structures on Euclidean four-space. Smooth h-cobordisms of three-manifolds are not well-understood either. D-brane models for dark energy given serious attention in physics seem to be extremely speculative; this whole area may be an opportunity for mathematicians, physicists, and computer sciences (interested e.g. in spin foam models) to benefit from talking to each other.

All the topics you list are interesting. You could have written a much better call for grant proposals than Mann’s. Yours would have clearly delimited this general range of inquiries without narrowing the focus down to one specific long-shot gamble: namely, settling the smooth Poincaré and using the answer to unlock the secrets of dark energy.

If Mann had asked around, he could have gotten advice that would have greatly improved DARPA’s call for proposals.

Maybe it’s still not too late — but I doubt it, since the deadline for submitting proposals has already been announced (4 pm ET, September 8, 2008).

Posted by: John Baez on December 29, 2007 9:34 PM | Permalink | Reply to this

### Re: Challenges for the Future

OK, I’ll have to be non-anonymous. Treating this as if Ben (yes, I know him personally) came up with this on his own (as opposed to being assigned it by DARPA higher up) and purely out of his own thoughts (as opposed to consulting while under a very tight time constraint) is attacking the messenger and very ad hominum at that. And then to assume he would be even more capricious in awarding grants…. Anyone want to volunteer to serve in his place?

Posted by: jim stasheff on December 30, 2007 1:33 PM | Permalink | Reply to this

### Re: Challenges for the Future

I suppose I did get a little carried away. I’m sorry for blaming Mann: someone at DARPA did something foolish and irresponsible in forcing/allowing this list to be used as a basis for the grant solicitation, but for all I know Mann was caught up by forces beyond his control and made the best of a bad situation. I shouldn’t have held him responsible.

Posted by: Anonymous #1 on December 30, 2007 8:03 PM | Permalink | Reply to this

### Re: Challenges for the Future

I agree with Anonymous #1 in thinking that this list of 23 supposed “challenges” is an “insult and embarrassment to the mathematical community”, and deserves tremendous negativity.

But isn’t DARPA the Research and Development organisation for the Department of Defense? I wouldn’t want their money anyway.

Posted by: Anonymous #2 on December 29, 2007 10:44 PM | Permalink | Reply to this

### Re: Challenges for the Future

Yes, DARPA is the Defense Advanced Research Projects Agency, an agency of the Department of Defense with an annual budget of \$3.2 billion, currently directed by Anthony Tether.

It has been suggested to me, via private email, that Mann was assigned to compose his list of problems, at very short notice, by the DARPA director. I don’t know what really happened. So, it may be unfair to blame Mann overmuch for any deficiencies of the DARPA Mathematical Challenges grant proposal solicitation.

Does anyone know how much money they plan to distribute? The importance of this whole issue is sort of proportional to that.

Posted by: John Baez on December 29, 2007 11:20 PM | Permalink | Reply to this

### Re: Challenges for the Future

Mann declares explicitly, “I am fully responsible for the selection and statement of these challenges”. It’s on the last page of the version of the challenges that’s on that curious parchment background.

So it may be fair to blame Mann quite a lot for the deficiencies of his list. That’s what taking responsibility is all about.

As for being assigned to compose this list at short notice, he did at least have time to consult this list of people:

“I would like to acknowledge the help of many mathematicians, especially Robert Calderbank, Gunnar Carlsson, Michael Deem, Eric Demaine, Yasha Eliashberg, Victor Eliashberg, Edward Frenkel, Alexander Gamburd, Robert Ghrist, Jack Morava, and Kari Vilonen for inspiration, suggestions, and corrections that have immeasurably improved my preliminary versions of this list.”

Posted by: Eugenia Cheng on December 30, 2007 2:21 AM | Permalink | Reply to this

### Re: Challenges for the Future

I agree with certain anonymous commenters and John that there’s quite a lot of flakiness in how the problems are expressed, and it’s certainly easy to believe on stylistic grounds that the document has just one author (and so I agree with Eugenia that surely he has some responsibility for said deficiencies and flakiness). On the other hand, the “I am fully responsible” sounds a bit like boilerplate, to protect his superiors up the chain of command. I bet someone up the chain of command had to approve this – that person, at the very least, shares in this as well.

Anyway, it could have been handled a lot better.

Posted by: Todd Trimble on December 30, 2007 1:30 PM | Permalink | Reply to this

### Re: Challenges for the Future

Hmmm… I often wondered what happened to the Hominidissiumus-project . Its founder Ew. Ger. Seeliger performed the first two experiments, but died too early to complete the third.

The first of them, performed 1922 in Bavaria, started with the “Handbook of Humbug”, a book designed to be confiscated. The following three years long trial caused nationwide excitement when Seeliger ordered “shitpeople” for witnesses like the Bavarian president of state, the catholic cardinal-archbishop and “the writer” A. Hitler. An interrogation of them should have proved the correctness of Seeliger’s naming of them. The court declared Seeliger as crazy and ordered him to be send into a mental hospital – where the physician begged him to leave because he was “too crazy for my institution”. According to Seeliger, the first Hominidissimus-Experiment was a complete success.

In the following years he traveled a lot, founded in New York the “Messias Foundation”, worked on a movie-adaption of “Peter Voss – the Thief of Millions” (one of the most successful films then in Germany) and observed sharply the rise of the Nazis (“Tratschional-Kotzialisten”). 1932 the 2nd Hominidissimus-Experiment was made. Seeliger distributed a parody (“The Howling for the Heil”) of a nazi-song in 10.000 copies in Berlin. After their seisure of power, Seeliger sheltered persecuted people and helped them to emigrate, e.g. the Feuchtwanger family. When he, at mayday 1933, put instead of the prescribed flag a flag-parody made of brownish paper and satirical comments (e.g. “every madness needs a flag”) onto his house, he himself became persecuted and fled into Switzerland. His friends in the resistance persuaded him to go back to Hamburg, where the Nazis were too frightened by his popularity to do him worse things than a publication-interdictum.

Until 1953, Seeliger lived very reclusive, turned towards past centuries – esp. the renaissance – and wrote never published novels about Erasmus v. Rotterdam. But the Hominidissimus-Project was not forgotten:

1953 - instead of 1957 as announced 1931 in New York – the third Hominidissimus-Experiment began with the publication of the baroque picaresque novels “Muchbeloved Falsette” and “Junker Schlï¿½rk”. Local district attorneys jumped forcefully into the trap and had to regret it. 1957 the Hominidissimus-Project should have led into a worldwide humorous scandal, set to trigger a “humorous world-revolution”. This step was never taken, Seeliger died 1959. Most of his manuscripts went lost, among them his autobiography and seven “Metacartoonfilms”. His movie mentioned above has been remade three or four times; the rest is forgotten.

Recent rumors suggest that his foundation in NYC still exists and pursuits the project in secrecy. May they have infiltrated governmental organisations?

Posted by: Thomas Riepe on December 30, 2007 4:43 PM | Permalink | Reply to this

### Re: Challenges for the Future

Sigh. I suppose might as well identify myself as yesterday’s unindexed anonymous poster.

I’m afraid this whole thread reminds me a little too much of the following story, from Tristes Tropiques, by Claude Lévi-Strauss : Part VIII, the Tupi-Kawahib

A widower had an only son, who was already almost grown up. One day he sent for him and told him that it was high time he got married. “What must I do to get married?” the boy asked. “It’s very simple,” his father said. “All you have to do is go and see our neighbors and try to get their daughter to like you.” “But I don’t know how to make a girl like me!” “Well then – play the guitar, and laugh, and sing her a song or two!” The son did as he was told. But as he arrived just as the girl’s father was dying, his behavior was thought to be most unsuitable and they drove him away and threw stones after him. He went home and complained to his father, who told him how he ought to behave in such cases. The boy went off to his neighbors again and arrived just as they were killing a pig. Remembering the latest of his lessons he burst into tears: “How sad! How good he was! How we loved him! We shall never find a better.” Once again the neighbors drove him away in exasperation. He described all this to his father, and once again was told exactly how to behave in such circumstances. When he paid his third visit, his neighbors were busy clearing the caterpillars from their garden. Always one lesson behind, he burst out with, “What an abundance of good things! May you have more and more such animals on your property! May they never be lacking!” And he was chased away again.

After this third rebuff the father told his son to build himself a hut. He went into the forest and cut down the necessary trees. A werewolf passed by in the night, thought the site a good one for himself to settle in, and went to work. The next day the boy came back to the clearing and found the work well advanced. “God is giving me a hand!” he thought to himself delightedly. And so they worked in double shifts, the boy by day and the werewolf by night. Before long the house was ready.

By way of house-warming the boy decided to feast off a roebuck. The werewolf preferred a human body. The one brought the buck by day, the other a corpse during the night. And when the boy’s father came along to join in the feast he saw a dead man on the table as pièce de résistance and said to his son, “Ah, my boy, I’m afraid you’ll never be up to anything much …”

Posted by: Jack Morava on December 30, 2007 6:27 PM | Permalink | Reply to this

### Re: Challenges for the Future

One might have hoped that the philosophy of science could have offered some suggestions as to the most rational way to distribute funds. But I can’t say philosophy’s own funding practices are too clever.

I can see that there’s a danger in wording proposals in a way that encourages what John calls ‘blather’ that you’ll tend to pick ‘low risk’ candidates, i.e., the well-established.

On the brighter side, perhaps you’re doing better than you did in the early nineteenth century when support for Abel and Galois was lacking (although the latter was always going to be an awkward case). Are there any cases of what we would now see as neglected mathematical geniuses of the twentieth century?

Posted by: David Corfield on December 30, 2007 11:23 PM | Permalink | Reply to this

### Re: Challenges for the Future

Allyn Jackson discusses the Darpa program (and mentions us) in April’s Notices.

Posted by: David Corfield on March 23, 2008 3:21 PM | Permalink | Reply to this
Read the post What has happened so far
Weblog: The n-Category Café
Excerpt: A review of one of the main topics discussed at the Cafe: Sigma-models as the pull-push quantization of nonabelian differential cocycles.
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