Should a General Relativitist Study Math Proofs?

[andytoh]

I know I posted a similar question before but it was moved to the Academic and Career Guidance section and so I got answers from many non-relativists who answered no because they weren't into theoretical physics.

So let me be more specific here. Would someone specializing in general relativity become better at general relativity if he studied the proofs of mathematical theorems that are used in general relativity? Some example mathematical theorems from Wald's General Relativity Book are:

-The Heine-Borel Theorem
-Frobenius' Theorem
-Noether's Theorem
-Paracompactness leads to the existence of partition of unity
-Hausdorff and Second Countable = paracompact
-{d/dx^1,...,d/dx^n} forms a basis for the tangent space Tp(M)
and the list goes on.

Would you say that studying the proofs of these theorems would make you better at general relativity? Being better at math means being better at general relativity right? Or is your time better off spent simply learning how to use them as tools for general relativity and not bother reading the proofs?

 

[mathman]

Would you say that studying the proofs of these theorems would make you better at general relativity? Or is your time better off spent simply learning how to use them as tools for general relativity and not bother reading the proofs?

As a mathematician (not a specialist in GR), I don't think you need to bother about understanding the proofs of the theorems you stated. The branch of mathematics you probably would benefit most from is differential geometry.

 

[andytoh]

Here's an earlier response by Chris Hillman that left me scratching my head:

"Right, you probably should insist on understanding.

I probably won't make any friends by pointing out the obvious: the fields you mentioned are highly competitive and use a lot of high level mathematics. Learning faster and retaining more surely than your peers would be an encouraging sign that such an area might be well suited to your talents. Conversely...

If you look at the Millenium problems, many of these have nothing to do with superstrings and can be completely stated in much more elementary mathematical language. Most would say that creativity is essential for attacking hard problems, not a huge store of background knowledge.

If you look at enough reviews of research papers, I think you'll see that most papers, even most good papers, are not trying to scale such Olympian heights. I think you can have a good career in math or physics without knowing much about all the stuff bandied about in string theory, you just should study other problems. If your reaction is that these problems can't be as interesting as "fundamental physics", I demur. My experience has always been that if you learn enough about any topic which has ever fascinated even one true born scholar, you too will agree that this topic is quite fascinating enough to spend a lifetime thinking about.

Many observers think that string theory and such like are vastly overpopulated. Even some of the wiser proponents of string theory have been heard to express concern about this "bandwagon effect".

I yak a lot about gtr, mostly because I happen to have taught myself a fair amount about this subject, tend to try to answer questions about things I know a lot about, and people tend to ask many questions about gtr. Now I doubt one could find a more enthusiastic fan of gtr than myself, but from time to time to I try to point out that there is a very very wide world out there, and there are many topics which IMHO are equally fascinating, but which throw up fewer stumbling blocks at the outset of study.
__________________
Chris Hillman"

 

[Chris Hillman]

Define "better" and "general relativity"

Would someone specializing in general relativity become better at general relativity if he studied the proofs of mathematical theorems that are used in general relativity?

It depends upon what you want to do in gtr.

If you want to work at the cutting edge, on questions involving global nonlinear stability, or the nature of "generic solutions" (e.g. Cosmic Censorship conjecture), you will probably need to master much hard analysis, the background for which includes much general topology, including many of the topics you mentioned and much much more. The reason for this is that this background is required for the theorems on PDEs, and techniques used to prove such theorems, which you will probably need to master.

(But if you have a really original idea, don't let that stop you from plunging in and trying to work it out!)

OTH, there are some useful things you can do which probably don't require much background in hard analysis.

BTW, some of the more algebraic results you mentioned are relatively trivial (no pun intended), so much of the background you might be concerned about mastering at first glance does not in fact pose a serious challenge.

is your time better off spent simply learning how to use them as tools for general relativity and not bother reading the proofs?

Hopefully you don't need to make an either/or choice!

But if you don't have a taste for hard analysis, but do have a taste for philosophical disputation, I have often mentioned that IMO philosophers of physics are woefully failing in their proper task, which is seeking out and criticizing sloppy thinking wherever it is to be found. At present (with one or two exceptions) these scholars confine their attention almost entirely to very narrowly defined "traditional disputes", where I feel they are simply marching around in circles and generally adding to the view that philosophers have little to offer to working scientists--- I don't agree, but I feel that philosophers have been spending their time very unwisely in the gtr literature.

If you are looking for easy pickings in classical gtr, here are two suggestions off the top of my head just in the area of finding and interpreting exact solutions, which tends to be both fun and easy:

1. I'd suggest learning about solution generating techniques, which look impressive (and are in fact rather fascinating) but which don't really require a huge amount of background to use--- for a good math or physics students, as few as one or two textbooks (e.g. books by Olver plus Belinksy and Verdaguer) might get you started.

2. I just mentioned colliding plane wave models in another thread; this is a fascinating and important topic in exact solutions which is easily learned from the monograph by Griffiths. They are of interest for at least two reasons: they are almost unique in being a highly tractable example of models of a physical interaction in fully nonlinear gtr, and they turn out to be applicable to the interesting question of black hole interiors.

Many topics in gtr do not require much beyond a solid background applied math type background in PDEs, plus a solid background in manifolds at the level of Lee's three GTM textbooks (Springer), plus of course gtr at the level of Weinberg, MTW, and a bit above most more recent textbooks.

It might help to point out that in my reply to mathwonk in another thread, I stressed that I generally agree with the view that too many authors of papers in gtr stress mathematical considerations and the expense of physical considerations, so perhaps the most important requirement of all is intelligent appreciation of the importance of avoiding physically inappropriate assumptions--- especially the tacit kind!

So please don't misinterpret my advice as an injunction to add to the bloated literature on physically questionable "solutions" of the EFE (if that is even a suitable term). I am suggesting that with a dollop of good sense, physically speaking, and comparatively little mathematical background, you can probably find some solutions which are not obviously absurd.

A possible topic which might be midway between "easy pickings" and really ambitious undertakings might be looking for yet another formulation of relativistic elasticity (something which has come up quite bit in PF in recent weeks, and from time to time is mentioned in the arXiv). Quite a few mathematical physicists have tackled this, and some imaginative approaches have been offered, but it seems fair to say that none of these have yet proven to be sufficiently useful for routine use, in comparison to say the literature on static spherically symmetric perfect fluid solutions. I guess there might be considerable opportunity here to demonstrate ingenuity and creativity without the need to acquire a great deal of background beyond stuff which many physics graduate students need to learn anyway. See http://www.arxiv.org/abs/gr-qc/0701055 for a light-hearted introduction (it is pleasant to observe that the author evidently took the trouble to write an engaging introduction, and did not try to disguise the limitations of his own contribution--- I wish everyone had as much consideration for the humble reader!)

 

[Chris Hillman]

Clarification

Hi again, andytoh,

Here's an earlier response by Chris Hillman that left me scratching my head:

As far as I recall, I had the impression that someone (not yourself?) appeared to be worrying (in another thread) about the daunting background required (seemingly) to follow current research in M-theory, and was trying to suggest that there is a Great Big Wide World out there, full of fascinating topics which require much less background to appreciate, and perhaps, to successfully attack.

 

[andytoh]

If you want to work at the cutting edge, on questions involving global nonlinear stability, or the nature of "generic solutions" (e.g. Cosmic Censorship conjecture), you will probably need to master much hard analysis, the background for which includes much general topology, including many of the topics you mentioned and much much more. The reason for this is that this background is required for the theorems on PDEs, and techniques used to prove such theorems, which you will probably need to master.

That sounds enticing enough. Thanks.

 

[Chris Hillman]

Mention someone actively working in this area

That sounds enticing enough. Thanks.

Well, if you're seriously interested, you should probably start reading papers in the field and perhaps contact an expert once you know more, e.g.

http://www.math.washington.edu/~pollack/research/research.html

 

[quantum123]

Would you more likely obtain a Physics Nobel Prize or a Mathematics Field Medal or none? I don't remember any Physics Nobel Prize being awarded for proving Maths theorems? In recent years, it seems that Nobel Prizes are awarded more and more towards applications in astronomy, astrophysics and cosmology. Maths is just a necessary evil, a tool that helps us to uncover secrets of the Universe and how it works - ie science.

 

[Chris Hillman]

Well, if your goal in life is to win a prize, I'd say you might be studying physics for the wrong reasons. If you think mathematics is evil, I'd say your chances of success in physics might be severely limited.

Maybe you just phrased your thought badly. How about this? Mathematics is the art of reasoning precisely and reliably about simple phenomena without getting confused. For this reason, mathematics is the scientist's best friend. Scientific issues sometimes eventually turn out to be "simple in essence", but they are almost always appear quite confusing at first! That is why scientists need a toolkit to help them cut through the underbrush.

A lot of modern mathematics comes down to reducing hard looking phenomena (like characterizing a topology) to computations which look very much like linear algebra, or even adding a bunch of products of plus and minus ones. (For those who know the buzzwords, computing a free resolution in homological algebra can be regarded as a clever trick to apply elementary ideas from linear algebra, and as a kind of common generalization of inclusion-exclusion from combinatorics and of the Euler characteristic. When Einstein quipped that "a theory should be as simple as possible, but no simpler" he was actually referring to a quantitative idea which comes down to exactly this: compute a free resolution in the case where this obviously is essentially the principle of inclusion-exclusion; or less ambitiously, compute the Hilbert polynomial of a certain module; the leading term gives the degree and dimension of an algebraic variety which is the Einstein wealth characterizing the "number of solutions" of some field equation.) In this sense, phenomena which come down to making such a computation are "in essence, simple". Discovering this, when it is true, requires following a possibly lengthy exercise in precise reasoning, without getting confused, i.e. it requires mathematics.

In his retirement address to the London Mathematical Society, Sir Michael Atiyah, who won a Field's medal and who had two students who also won a Field's medal (roughly equivalent to winning two Nobel Prizes and supervising students who won four Nobel Prizes), stressed one of my favorite themes, the role of suprising connections between seemingly very different phenomena.

For example, techniques (see "Groebner basis") which are perhaps best learned in the context of algebraic geometry turn out to be very useful for certain counting problems (see "Schubert calculus" in some of the Weeks at John Baez's website) and for solving nonlinear systems of coupled partial differential equations (see "differential rings" and "symmetry analysis"). The rather abstract notion of sheaves turns out to be a natural meeting ground for analysis, algebra, topology and logic, and is currently being used in the quest for quantum gravity. The ideas of K-theory have found application in the landmark Atiyah-Singer theorem which in turn is important for modern physics, and also provide important invariants for dynamical systems theory, and have many other applications to mathematics and thus to fields where advanced mathematics can be profitably applied. Just a few examples off the top of my head...

This theme was also stressed by Feynman in his Lectures on Physics (see his discussion of the many ways in which certain ODEs arise in physics).

 

[quantum123]

It is true that the Nobel committee award people who build hard-tools like microscope and telescope and even computers , rather than people who build soft-tools like maths. Perhaps such a bias should be pointed out to people who want to embark on a career in science. There is a general agreement among people that maths is NOT science. If you can prove that 1+1=2, you don't necessary know much about how the universe works.(Some people like Penrose thinks otherwise). Poincare, Noether and Minskowski were never awarded any Nobel prizes. Maths is beautiful and you can get stuck inside your entire life because of a faulty scientific idea.(String theories?) Why not let others do the dirty work - Einstein was not a differential geometer? He just need to consult one. I am still waiting to see if Hawking and Penrose can get a Nobel prize.

 

[Chris Hillman]

What, not even an IMHO?

Hi quantum123, have you considered adding a signature to your PF profile, so that your posts appear with a tag saying that your posts express personal opinions which may be controversial? (or words to that effect...)