Double deformation

As if deforming your mathematics in one parameter weren't enough, they're now doing it in two. So p, q deformed integers are [n]_p,q = (pⁿ - qⁿ)/(p - q). Time to go through weeks 183-188 of This Week's Finds to see if there's any categorification to be had. This reminds me of an idea I had when reading in week 184 about the Euler characteristic of complex flag manifold in n dimensions being n!. Noting from p. 67 of Cartier's excellent Mathemagics paper that infinity factorial is the square root of 2.pi, can we conclude that the Euler characteristic of the infinite-dimensional complex flag manifold is the square root of 2.pi? Stranger things happen here.

David Mumford

David Mumford is perhaps most famous in the mathematical world for his work in algebraic geometry,which earned him a Fields Medal, and for the lecture notes which became The Red Book of Varieties and Schemes. Here at last for those with a penchant for geometric thinking was a way to get a handle on schemes. He modestly describes his own "small contribution to schemes" was to publish there

...a series of 'doodles', my personal iconic pictures to give a pseudo-geometric feel to the most novel types of schemes. What was at the back of my mind was whether or not I could get my own teacher Zariski to believe in the power of schemes.

Mumford swapped fields in the 1980s and has since worked on pattern theory, especially as applied to computer vision, but he continues to contribute to mathematical exposition. His course on Modeling the World with Mathematics looks excellent. I only wish I'd attended something like that in my teens. And Indra's Pearls would be a great book to receive for those a little further up the mathematical ladder.

I want to look here a little at a couple of talks he has given at prestigious mathematical events. First, there is The Dawning of the Age of Stochasticity delivered at a meeting held in Rome in 1999, Mathematics Towards the Third Millennium. (Though not of course mathematics' third millennium.) After presenting probability and statistics as a component of mathematics dealing with chance, just as geometry deals with our experience of space, analysis the experience of force, algebra that of action, Mumford goes on to say something stronger - that thought itself is better captured by probability theory than by logic. What seems to be evident from the experience of those working in artificial intelligence is that this is right. It's hard to think of a domain other than automated theorem proving where a statistical approach is not winning over a logic based approach. Even here, this might be through insufficient effort. As I mention in chapter 4 of my book, George Polya developed a Bayesian interpretation of mathematical conjecture assessment, and went on to talk about the assessment of the plausibility of potential paths to a proof.

Mumford also points to the increase of stochastic concepts within maths itself, such as random graphs and stochastic differential equations. There are plenty of other examples he could have chosen such as random matrices, random polynomials, and random groups. The most controversial part of the paper is his suggestion that random variables be put "into the very foundations of both logic and mathematics" in order to "arrive at a more complete and more transparent formulation of the stochastic point of view" (p. 11). This may be a step too far, but it's worth considering chance-like phenomena in mathematics. When I was thinking hard about what Bayesianism had to say to mathematics, I became intrigued with the distribution of mathematical constants. Looking at those tables, especially the one for mixed constants, brought to mind Benford's law - that the first digits of data from a random variable covering several orders of magnitude satisfies Prob(first digit = n) = log₁₀((n + 1)/n). Try it for the areas of countries in square kilometers. For example, roughly log₁₀(6/5) or 7.9% of them have areas beginning with a 5. The usual justification for this is that we wouldn't expect the answer to differ had we used a different unit of measure, such as square miles, so we need a distribution of first digits which is invariant under scalar multiplication. A uniform distribution over the fractional part of the logarithms of the data does the trick. But if some categories of mathematical constant also show this distribution, the same argument wouldn't go through. Possibly one could argue that the distribution should have the same form if we worked in bases other than 10. In any case, why the fluctuations? Why that little kink around the early 2000s in the mixed constants table?

Two years after the Dawning paper Mumford wrote Trends in the Profession of Mathematics. A couple of points I like in this are, first, his advocacy of a second criterion to judge someone's contribution to mathematics, other than theorem proving. This is what he calls defining a model. Here one extracts what is essential to a situation by modelling it in such a way that the simplest examples embody what is most significant. Examples he gives are the notion of the homotopy type, the Ising model, and the Korteweg-deVries equation.

PhDs and jobs should be awarded for finding a good model as well as for proving a difficult theorem.

Second, there is a clear statement of the kind of view of the interaction of pure and applied mathematics that I was driving at in this post:

...there is continuous mixing of pure and applied ideas. A topic, such as the Korteweg-deVries equation, starts out being totally applied; then it stimulates one sort of mathematical analysis, then another. These developments can be entirely pure (e.g. the analysis of commutative rings of ordinary differential operators). Then the pure analysis can give rise to new ways of looking at data in an experimental situation, etc. Topics can be bounced back and forth between pure and applied areas.

I think we can safely say that Mumford may claim, along with Thurston, “I do think that my actions have done well in stimulating mathematics.” (‘On Proof and Progress in Mathematics’, Bulletin of the American Mathematical Society, 1994, 30(2): 177).

Update: Another graphic of over 200 million constants shows more Benford-esque behaviour, although even this one seems to flatten out a little too quickly for const/x. A place to start might be to ask why on the first page of graphics the rationals behave as they do.

Articulating your program

Ronnie Brown has a paper out today, Three themes in the work of Charles Ehresmann: Local-to-global; Groupoids; Higher dimensions, delivered at a conference in honour of Ehresmann. Brown wrote some excellent expository pieces advocating the use of groupoids, which were very useful to me while writing the ninth chapter of my book. He has a page describing the story of his long-running program - higher dimensional group theory - which includes some good points for philosophers to mull over. For example, he outlines the Criteria for success for a mathematical theory as follows:

• 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.

He notes that higher dimensional group theory has succeeded well in all of these criteria except the last one, which he doesn't rate very highly. I would agree. To some extent such problems become famous for rather contingent reasons. On the other hand, to their credit, they can help assess how a program is doing in the sense that, even if they are not especially significant in themselves, they would seem to require that a deeper level of understanding be achieved if they are to be solved. 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.

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.

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.

From his major problems page:

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 articulating why they 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.

Like 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.

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'.

Philosophy of physics

During my year long teaching post at Oxford (2002-3), I spent most of my time with the philosophers of physics there. Philosophers of physics tend to be much more au fait with contemporary physics than philosophers of mathematics are with mathematics. Worringly for us philosophers of mathematics they tend to know more mathematics too. One piece of evidence for these last two assertions is the 202 page paper Algebraic Quantum Field Theory by Princeton philosopher Hans Halvorson (including a 61 page appendix on reconstructing groups from their categories of representations type results by Michael Müger). This is to appear in Handbook of the Philosophy of Physics edited by Jeremy Butterfield and John Earman. In this paper Halvorson identifies himself with analytic philosophy:

In philosophy of science in the analytic tradition, studying the foundations of a theory T has been thought to presuppose some minimal level of clarity about the referent of T. (Moreover, to distinguish philosophy from sociology and history, T is not taken to refer to the activities of some group of people.) In the early twentieth century, it was thought that the referent of T must be a set of axioms of some formal, preferably first-order, language. It was quickly realized that not many interesting physical theories can be formalized in this way. But in any case, we are no longer in the grip of axiomania, as Feyerabend called it. So, the standards were loosened somewhat—but only to the extent that the standards were simultaneously loosened within the community of professional mathematicians. (pp. 3-4)

So philosophers should study AQFT because:

AQFT is our best story about where QFT lives in the mathematical universe, and so is a natural starting point for foundational inquiries.

That parenthesised sentence in the first of the quotations above worries me, since it seems to me to express a sentiment that will forever condemn philosophy of mathematics to avoid serious engagement with the activities of practicing mathematicians. On pp. 4-5 of my book I raise the question as to why the philosophies of physics and mathematics have such differing relationships to the discipline each studies, and suggest that much of the difference is due to events in the history of analytic philosophy and the role it assigned to logic in philosophical analysis. I expanded on this in a review of Martin Krieger's Doing Mathematics. There I am critical of some parts of philosophy of physics for not realising the extent to which they have diverged from analytic philosophy. Most philosophers of physics avoid confrontation with that section of the analytic heartland know as metaphysics, but it is striking that when they do, they often reveal very large problems, such as when Jeremy Butterfield confronts David Lewis's metaphysics with the fact that it is incompatible even with classical mechanics. Personally, I feel the best way to frame what philosophers of physics are doing when they think hard about the presuppositions of physical theories is what R. G. Collingwood described as engaging in metaphysics. In an earlier post, I outline this in terms of what I call the Historical Stance with reference to the Empirical Stance of Bas van Fraassen, another Princeton Philosopher.

Against Halvorson, we cannot separate a theory from the socially-embodied arguments in which its adherents and opponents engage. To the extent that Halvorson has done something worthwhile in writing this long paper, it will modify the thinking of people working in and around quantum field theory. Once we realise this, mathematics seems strikingly similar, full of extended conversations and arguments. I shall end with the moving remarks of Ross Street, an exponent of my favourite mathematical research program, from his talk at the IMA n-categories workshop:

For so long I have felt rather apologetic when describing how categories might be helpful to other mathematicians; I have often felt even worse when mentioning enriched and higher categories to category theorists. This is not to say that I have doubted the value of our work, rather that I have felt slowed down by the continual pressure to defend it. At last, at this meeting, I feel justified in speaking freely amongst motivated researchers who know the need for the subject is well established.

Applicability of mathematics: special functions

I've just read an interesting paper by Robert W. Batterman - On the Specialness of Special Functions (The Nonrandom Effusions of the Divine Mathematician). Here's an extract:

...it seems reasonable to maintain that many special functions are special for more than simple pragmatic reasons. They are not special simply because they appear in the physicist’s, applied mathematician’s, and engineer’s toolboxes. Furthermore, special functions are not special simply because they share some deep mathematical properties. Recall this is the point of view of Truesdell and of Talman/Wigner. On their proposals, what makes some functions special is that despite “surface” differences, they are each solutions to the “F-equation” (for Truesdell), or they possess similar group representations (for Talman and Wigner). While these classificatory schemes suffice to bring some order to the effusions of the Divine Mathematician, they do not fully capture the special nature of the special functions.

From the point of view presented here, the shared mathematical features that serve to unify the special functions—the universal form of their asymptotic expansions—depend upon certain features of the world. What Truesdell, Talman and many others miss is how the world informs and determines the relevant mathematical properties that unify the diverse special functions.

As I noted, in many investigations of physical phenomena we find dominant physical features—those features that constrain or shape the phenomena. These are things like shocks and the highly intense light appearing in the neighborhood of ray theoretic caustics. They are features that are most effectively modeled by taking limits.

Limiting idealizations are most effective for examining what goes on at places where the “laws” break down—that is, at places of singularities in the governing equations of the phenomena. These “physical” singularities and their “effects”—how they dominate the observed phenomena—are themselves best investigated through asymptotic representations of the solutions to the relevant governing equations. The example of the Airy integral is a case in point. By using Stokes’ asymptotic representation we get superb representations of the nature of the diffraction relatively far (large z) from the dominating “physical” singularity—the caustic.

There's a curious tendency when it comes to discussing the applicability of mathematics to polarise one's response to the question of which of mathematics and science owes the other the most. It seems each side is only too happy to exaggerate the role of their favoured discipline, finding the benefits mathematics bestows as miraculous, or deflating mathematics to a bunch of tautologies which physics is gracious enough to give an interpretation to. In the philosophical literature of the past century, with one or two notable exceptions, the latter attitude has been prevalent. Of the two, it is the role of mathematical understanding which tends to get passed over or taken for granted.

Batterman is more sensitive to the narratives various mathematicians and physicists tell about special functions, but I wonder if there might not be a richer mathematical story which would make the still sharp dichotomy he maintains between physical and mathematical considerations less sharp. Is it not possible that the richer mathematical understanding of special functions gained since Talman (1968) could intersect with the physical considerations treated by Batterman? For instance, might the asympotic results he discusses have something to do with current ideas from the group representation understanding of special functions? And how do q-deformed special functions fit in? It's surely common to find mathematics and physics narratives creatively intertwined.

Batterman concludes:

I hope that the discussion here leads us to question the anthropocentric role of the mathematician’s appreciation for beauty (or formal analogy) as an important criterion for what arguably should be paradigm examples of mathematics’ applicability to the world; namely, the special functions.

I'd like to hear some contemporary mathematicians' aesthetic narratives about special functions.

Making reference

Further nuances appear today in the statistical analysis of the Riemann zeta zeros. The evidence looks strong for the conjecture that in the limit as one climbs the line Re(z) = 1/2, the distribution of normalised spacings between zeros tends to that of the eigenvalues of large random matrices from the Unitary Ensemble. Bogomolny and colleagues show how as we pass up Re(z) = 1/2 away from the real axis, the deviation from the asymptote resembles that of the distribution of eigenvalues from finite dimensional matrices. They calculate the effective dimension of these matrices in relation to the height above the real axis, and verify their claims by studying batches of zeros, including some around the 1.3 x 10²² th. Elsewhere, the first ten trillion consecutive zeros have been checked.

There's plenty to interest a philosopher about this work - e.g., Would it be right to say that with the advent of computers mathematics has become 'empirical'? - but the issue I raise in my 'Mathematical Kinds' paper (p. 22) points elsewhere. There's a huge amount of work going on aimed at explaining why the Riemann zeros are distributed as they are. Berry and Keating observe:

… three areas of mathematics and physics, usually regarded as separate, are intimately connected. The analogy is tentative and tantalizing, but nevertheless fruitful. The three areas are eigenvalue asymptotics in wave (and particular quantum) physics, dynamic chaos, and prime number theory. At the heart of the analogy is a speculation concerning the zeros of the Riemann zeta function (an infinite sequence of numbers encoding the primes): the Riemann zeros are related to the eigenvalues (vibration frequencies, or quantum energies) of some wave system, underlying which is a dynamical system whose rays of trajectories are chaotic.

Identification of this dynamical system would lead directly to a proof of the celebrated Riemann hypothesis. We do not know what the system is, but we do know many of its properties, and this knowledge has brought insights in both directions...

Berry B. and Keating J. (1999) ‘The Riemann Zeros and Eigenvalue Asymptotics’ SIAM Review, 41, No.2 , 236-266.

What are we to make of the sense they give that there is a dynamical system, a mathematical entity, many of whose properties are known, but which is not yet completely identified? Similar themes have debated in the philosophy of science - e.g., when should it be said that a scientist made proper reference to the electron? Here, if Berry and Keating's system is later identified, what will decide whether they had already made reference to it? Another excellent case study would look at the question of when it could be said that sufficient theoretical resources had been provided to make reference to the monster group. Merely conjecturing that there is a largest sporadic finite simple group would surely not suffice. On the other hand, now, even if we don't yet completely understand it, we clearly have it pegged.

Mathematics and first principles

Denis Lomas, who has written a review of my book for MAA Reviews (members only), recently reminded me of a review, Mitteleuropa am Aldwych, written by the philosopher Ian Hacking of a book of correspondence between Paul Feyerabend and Imre Lakatos. Lakatos may best be known to you for his dialogue Proofs and Refutations in which a teacher and students argue about the meaning and proofs of the Euler conjecture that for a polyhedron V - E + F = 2, the letters standing for the number of vertices, edges and faces. Here is Hacking:

Lakatos's contribution to the philosophy of mathematics was, to put it simply, definitive: the subject will never be the same again. For decades the philosophy of mathematics was about foundations, set theory, paradoxes, axioms, formal logic and infinity - an agenda set by Bertrand Russell, among others, beefed up by the truly wonderful discoveries of Kurt Gödel. Lakatos made us think instead about what most research mathematicians do. He wrote an amazing philosophical dialogue around the proof of a seemingly elementary but astonishingly deep geometrical idea pioneered by Euler. It is a work of art - I rank it right up there with the dialogues composed by Hume or Berkeley or Plato.

Praise indeed, and yet elsewhere, as I commented at pp. 7-8 of a paper discussing Michael Friedman's Dynamics of Reason, Hacking describes Lakatos as a 'deflator' when it comes to mathematics. By this he means that Lakatos is showing that as mathematics proceeds, if it is carried out properly with plenty of critical discussion, a point will be arrived at where the definitions are such that results will follow easily from them. A theory which was initially driven by (quasi)-empirical facts has become merely a collection of analytic statements, true by virtue of meaning. Now, I think this is to get Lakatos very wrong, as I suggest on p.8 of the Friedman review. Yes, it's all about having good definitions, but they're good for Lakatos to the extent that they're right, or at least more right than their predecessors.

Urs Schreiber and I have been discussing related ideas about when one feels one has understood a construction properly. The strange thing is that there's almost a disincentive to reformulate a field to make it as well-organised as possible so as to allow a principled understanding. Some of this may be down to the temporary advantage you'll gain if you alone thoroughly grasp a field and can produce a string of new results which appear to your rivals to be arrived at rather mysteriously. But there's also this other issue that you will be thought to have made the results of the field trivial, or true simply in virtue of meaning.

I don't recall anywhere Lakatos providing us with the philosophical resources to help us ward off the charges of deflation or trivialisation. Instead, I think we should look to Alasdair MacIntyre's revival of Aristotelianism, in particular pages 184-5 of MacIntyre A. (1998) 'First Principles, Final Ends and Contemporary Philosophical Issues' in K. Knight (ed.) The MacIntyre Reader, Polity Press, pp. 171-201. This paper will appear in the first of two volumes of collected papers with Cambridge University Press this April. It's no easy matter to read an extract from one of his papers from a standing start, but here is a taste of what he says:

That first principles expressed as judgments are analytic does not, of course, entail that they are or could be known to be true a priori. Their analyticity, the way in which subject-expressions include within their meaning predicates ascribing essential properties to the subject and certain predicates have a meaning such that they necessarily can only belong to that particular type of subject, is characteristically discovered as the outcome of some prolonged process of empirical enquiry. That type of enquiry is one in which, according to Aristotle, there is a transition from attempted specification of essences by means of prescientific definitions, specifications which require acquaintances with particular instances of the relevant kind (Posterior Analytics, 93a21-9), even although a definition by itself will not entail the occurrence of such instances, to the achievement of genuinely scientific definitions in and through which essences are to be comprehended. (184)

...the analyticity of the first principles is not Kantian analyticity, let alone positivist analyticity. (185)

MacIntyre goes on discuss truth in terms of adequacy of the intellect to its subject matter. Clearly relating these ideas to mathematics needs an extended treatment, beyond what I have given in my How Mathematicians May Fail to be Fully Rational, e.g., pp. 12-13.

More material for a philosophy of real mathematics

I hope I didn't give the impression in the last post that I think there's little mathematical exposition to be had. There could always be more, and what there is could be better organised, but there are plenty of shiny pebbles lying about for us to pick up. From today's Derived categories of coherent sheaves by Tom Bridgeland:

In the usual approach to the study of algebraic varieties one focuses directly on geometric properties of the varieties in question. Thus one considers embedded curves, hyperplane sections, branched covers and so on. A more algebraic approach is to study the varieties indirectly via their (derived) categories of coherent sheaves.

So, two approaches to the study of varieties. Why would we prefer the latter?

Firstly, algebraic geometers have been attempting to understand string theory. The conformal field theory associated to a variety in string theory contains a huge amount of non-trivial information. However this information seems to be packaged in a categorical way rather than in directly geometric terms.

For a summary of one group's approach to the category theoretical formulation of conformal field theory, read Categorification and correlation functions in conformal field theory.

A second motivation to study varieties via their sheaves is that this approach is expected to generalise more easily to non-commutative varieties. Although the definition of such objects is not yet clear, there are many interesting examples. In general non-commutative objects have no points in the usual sense, so that direct geometrical methods do not apply.

This points us to the non-commutative geometry programme (or programmes). A philosopher of geometry wanting to understand the relationship between Connes' and Grothendieck's visions of space might begin with Pierre Cartier's A Mad Day's Work.

A third reason is that recent results leave the impression that categorical methods enable one to obtain a truer description of certain varieties than current geometric techniques allow. For example many equivalences relating the derived categories of pairs of varieties are now known to exist. Any such equivalence points to a close relationship between the two varieties in question, and these relationships are often impossible to describe by other methods. Similarly, some varieties have been found to have interesting groups of derived autoequivalences, implying the existence of symmetries associated to the variety that are not visible in the geometry.

This points us to the theme of mathematical reality.

Four very rich paragraphs.

In praise of exposition

If one takes seriously my philosophical position, that understanding is the aim of mathematics, one is led to think that expository writing is crucial to the mathematical enterprise, and that in many ways it is more important than the journal articles which rigorously prove the results covered by that writing. To forestall the usual criticisms, let me be clear that this is not to deny the importance of proof, or to be in any way dismissive of the achievement of a robust rigour over the centuries. Indeed, the level of rigour achieved by contemporary mathematicians provides a stable framework in which understanding can flourish. It is to say, however, that without the understanding transmitted face-to-face from teacher to student, and all too rarely captured in print, mathematics collapses.

I come then to praise exposition, and for an example will consider a piece recently brought to my attention, written by Jacob Lurie and titled A Survey of Elliptic Cohomology . If we take this survey as at least as worthy of philosophical attention as any stretch of definitions, lemmata, and theorems from a journal paper, we are brought to pose ourselves a rather different set of questions. First, what kind of writing does it most resemble? A story might be the best one word answer. Second, who is it addressed to? Clearly not just anyone. You must have some training in various branches of mathematics, although the audience ranges from those like me whose mathematical understanding is being stretched to breaking point during various passages (even with the help of Week 197, and references therein), to those for whom it is just an exercise in shaping what they largely already know. Either way, it is clear that to participate as a mathematician you need to train in it as you would a craft. Third, what are we to make of the language employed by Lurie? To take a couple of examples from page 10:

Many of the cohomology theories which appear "in nature" extend in a natural way to equivariant cohomology theories.

There are some respects in which Borel-equivariant cohomology is not a satisfying answer to our question.

What needs to be undertaken here are textual analyses. I made a start on the use of in nature and natural in chapter 9 of my book. For a longer passage, one might look at Lurie's final paragraph:

Unfortunately, our algebraic perspective does not offer any insights on the problem of where to find such a cohomology theory in geometry. Nevertheless, it seems inevitable that a geometric understanding of elliptic cohomology will eventually emerge. The resulting interaction between algebraic topology, number theory, mathematical physics, and classical geometry will surely prove to be an excellent source of interesting mathematics in years to come.

'Insights', 'inevitable', 'geometric understanding', 'interesting' - there's plenty of work to be done.

Blog troubles

I shall certainly be taking Urs' advice to change software when I have the time. At the moment, under the post 'Category theory and ontology' it shows '1 comment'. If you click on this you are shown Kea's comment, making reference to one by John Baez, which doesn't show. Here was John's comment:

David writes:

I strongly suspect that category theory will prove to be the only viable language to cope with the subtle relations of sameness involved here in computer science, and also elsewhere.

Lots of category-theoretic computer scientists have felt this for a long time: the way they put it, proof theory should take the poset of propositions, where the order relation

P -> Q

is implication, and see it as a quotient of some more interesting category where there can be lots of morphisms from P to Q, namely the different proofs that P implies Q.

They've worked this out in great detail in the case of intuitionistic logic, using cartesian closed categories. They've also done it for linear logic, using *-autonomous categories.

Interestingly, it's a lot harder for classical logic! For a long time it was believed that if you take a cartesian closed category and throw in relations that make it classical, it automatically collapses down to a mere poset - namely, a Boolean algebra.

But here in Marseille I've met someone who apparently succeed in getting around this problem: Peter Selinger. In his work on "control categories" (whatever the hell those are), he supposedly succeeded in finding nice categories where the morphisms are proofs in classical logic.

Both he and I will be here all throughout February, so I'm hoping I'll actually learn what this is all about. I'm also hoping he can explain linear logic to me, because I've never understood that. Part of the problem, I now realize, is that I don't have a feel for *-autonomous categories.

Category theory and ontology

I've long harboured the hope that the rise of category theory will push philosophy in interesting directions, and this in two ways: (1) Providing metaphysics with new tools; (2) Making us think harder about the nature of enquiry if a 4000 year old discipline continues to seek to improve its basic language. Concerning (1), it wouldn't surprise me if much of the category theoretic 'metaphysics' gets done by computer science people and physicists. After all, database theorists have to deal with quesions of type and identity all the time. During the IMA n-categories workshop, Michael Johnson gave John Baez and me a fascinating lesson in all this along the banks of the Mississippi.

Today the ArXiv has on offer Towards a Definition of an Algorithm by Noson S. Yanofsky. Defining the concept of an algorithm is surprisingly hard. It's easy enough to give examples of programs you'd want to say carried out the same algorithm, but how would you make the equivalence relations of sameness explicit in the following schema?

Discipline          Objects

Programming         Programs

Computer Science    Algorithms = Programs/~

Mathematics         Computable Functions = Algorithms/~

It sounds like a great topic for a philosopher, and indeed we are pointed to: W. Dean. What algorithms could not be. 2006 Thesis in Department ofPhilosophy. Rutgers University.

Yanofsky goes on to say:

Whether or not two programs are essentially the same, or whether or not a program is an implementation of a particular algorithm is really a subjective decision. We give relations that most people can agree on that these two programs are "essentially" the same, but we are well aware of the fact that others can come along and give more relations. (p. 3)

There's a danger in using the word 'subjective' of decisions to mean one can't at present decide in a way that one thinks won't be challenged in the future. For one thing, much of what you say will have to be given this label, with its relativist connotations. I've never much liked the epithet as used in Subjective Bayesianism to distinguish a position which simply requires our degrees of belief to satisfy the probability axioms, in opposition to Objective Bayesianism where given an agent's state of knowledge there is one rational choice for their degrees of belief. The term almost lends itself to the criticism sometimes heard from non-Bayesians that Bayesians could lock themselves up in a dark room and feel happy, safe in the knowledge that their degrees of belief are coherent. Subjective Bayesians can still think there is a duty upon them to find out what they can and make responsible assessments of plausibilities. Michael Polanyi's choice of 'personal' in Personal Knowledge relates strongly to this sense of responsibility. For some comments on Polanyi see my November 12 post.

Back to category theory, according to Yanofsky, 'The category of algorithms is the initial free category with a strict product that is closed under recursion (i.e., has a natural number object).' I strongly suspect that category theory will prove to be the only viable language to cope with the subtle relations of sameness involved here in computer science, and also elsewhere. For more about category theory and computation, check some of the lectures in the Geometry and Computation programme.

Furthering the project of categorifying physical ontology, Aaron D. Lauda and Hendryk Pfeiffer have just written State sum construction of two-dimensional open-closed Topological Quantum Field Theories .

Blogging matters

Does anyone know how to provide a Blogger blog with a more sensible way of recording recent comments than the one they've provided? Even a recent comment to a previous post might not show up. E.g., John Baez recently commented here on what he meant by "very few of our most successful theories of physics have been given a fully rigorous foundation... not even Newtonian gravity for point particles!"

Elsewhere, it's interesting to see other blogging philosophers of mathematics heading in a "real mathematics" direction. Over on Antimeta, Kenny Easwaran claims "Although we often think that theorems are the main product of mathematics, it seems that a lot of the time just identifying the "right" structures to be talking about is really the goal."