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While the claim of an axiomatics is making the bigger public impact, this is not what drives the development.
What drives the development is understanding interacting full non-perturbative quantum field theory, problems of the kind that the Clay Millenium Problem asks for.
Doing so requires dealing with global quantum anomaly cancellation. Deep problems of global quantum anomaly cancellation in low dimensional quantum field theory made Freed, Hopkins and others realize that (higher) gauge fields have to be described as cocycles in differential cohomology. But there remained open technical issues.
Based on my PhD thesis work I had made the rather natural observation that a proper formulation of differential cohomology takes place in higher topos theory. A few years later, in his 2011 talk at the Simons center, Hopkins said that this is how his seminal article on differential cohomology with Singer “should have been written”. When applying this to open problems in field theory it dawned on me that actually there is a simple axiomatics in a higher topos which gives the theory of differential cohomology (thanks to hints from Richard Williamson, who is back on the nForum these days). By the way, regarding your PPS this is formalized in HoTT.
In fact the axioms are better than I even realized. Recently Bunke-Nikolaus-Völkl observed that where I wrote “differential cohomology in a cohesive $\infty$-topos” one is entitled to write “differential cohomology IS cohesive $\infty$-topos theory”. Using this they now solved some remaining open technical issues in the quantum anomaly cancellation of the type II superstring (still unpublished, but let know if you want to hear details), following Distler-Freed-Moore.
Regarding higher category theory in physics: it is a fact that the locality of $n$-dimensional field theory is incarnated in monoidal $n$-category theory. That’s how it comes about.
Regarding the mysteries of quantization: what I have to offer on these is here.
I am not sure if we are communicating. Above I highlighted how this is all about understanding physics questions.
Perhaps the problem is in the phrase “physics questions”. I spoke to some colleagues in the fluids research group a while ago and got the impression that they didn’t think the Navier–Stokes millennium problem was relevant to their work – they regarded it as a question in PDE theory.
@sure, let me weigh in, as another physicist. It seems to me that you have already answered your question, in the negative. From what I understand, your view (which I do not necessarily agree with) is that QM and QFT are not “well founded” and are likely to be replaced with something different, just like the geocentric model was replaced by the heliocentric one. Your question then sounds to me as follows: can mathematical investigations into the structure of QFT help one find this eventual replacement? Of course, nobody can answer that with a certain Yes or No, simply because nobody knows whether any such replacement exists and, if it does, how it is to be found. However, most active mathematical investigations of QFT, including the directions that Urs alluded to earlier, do not have the overthrow of QFT as a primary goal.
So, if you are indeed focused on finding alternatives to QFT, then you’d have to look elsewhere for answers. That is, unless, you’d be satisfied by stumbling onto such answers by accident. But in that case, of course, it won’t really matter what you choose to study.
re the last question in#6:
Yes. Of course to discuss this you need to recognize a modern fundamental physics breakthrough. Your emphasis of Newton’s laws above reminds me of my theoretical physics profs back then who would teach us classical mechanics from Goldstein’s book and not know about symplectic geometry. They were still leaders in their respective fields and would not see the need to modern more fine-grained insights into the laws of physics.
But when it comes to fundamental high energy physics there has been some progress in the centuries since, and the modern questions range deeper. That one needs the language of mathematics to talk about them, and not philosophical principles as you suggest, is an empirical fact of life which you won’t have much luck with fighting against.
The big open question in modern fundamental physics is the UV-completion of the standard model plus gravity. (Any remaining doubts about this were disspelled just a few days back by bicep2.) The main contender here is string theory. Building a model here means building a string vacuum, which in turn means to build a 2d SCFT of central charge 15, well defined on all genera.
The subtlety of accomplishing this is widely underappreciated in the physics community, due to the wide-spread lure of those philosophical principles that you appeal to.
I know the kind of attitude well which you seem to be displaying. Back when I was in Hamburg and my boss would speak to the local string theorists about his classification of rational 2d CFT they (some) would yawn and suggest that they knew all this 20 years back. But they didn’t, they just followed the custom in theoretical physics to declare any widely held believe after a few years a fact. The actual fact is that the full classification revealed that some of the modular invariant CFTs in the literature extended in more than one way to a full 2d CFT, while other’s didn’t at all. Given that each of these is a potential part of a stringy UV completion of the standard model, this matters.
Now most string vavua are built not even algebraically like this but geometrically, via sigma-models. This is even more dangerous. Sometimes it is good to remember that nobody has much of an idea if the notorious string vacua landscape actually exists the way commonly thought, since very little is known for sure about which of its conjectured points actually exist as full CFTs.
The reason that this is subtle is that there are, as I mentioned above, famous and famously subtle global quantum anomaly cancallation conditions obstructing the existing of what naively may look like a consistent superstring background. Staggeringly, an argument for what actually the full consistency condition on a type II background really is was advanced only in 2009, by Distler-Freed-Moore.
(I said this and the following already in my first message, but I suppose the point was lost. I urge you to actually look at this material if you are really interested in a discussion. See their very last remark, for emphasis.)
Now this quantum anomaly cancellation requires the string’s background gauge fields to be cocycles in certain twisted versions of differential cohomology. But it wasn’t entirely clear what the right concept of twisted differential cohomology here really is. This missing ingredient was recently provided by Bunke-Nikolaus-Völkl, based on axiomatic cohesion.
One can actually nicely motivate the axioms of cohesion from deep philosophical principles, which you say physics is about. But once one has the axioms formulated mathematically, one is to study the mathematics to find out what a consistent superstring background is, which then has a chance of providing a consisten UV completion of the standard model plus gravity.
There are more stories like this. Maybe just very briefly: a big discussion in fundamental physics these days concerns the quantum gravitational behaviour of black holes. These arguments stack vague ideas on top of conjectures on top of vague ideas based on the AdS/CFT duality conjecture. At the same time almost nothing precisely is known about how holography actually works in this case. Now, using the extended local QFTs (the ones I mentioned require higher category theory for their description) one may precisely capture at least the higher CS/WZW variants of holographys and study these. Quite a few of the widely held claims about holography turn out to at least receive qualification in these precisely understood examples. I hope it is clear that by running this backwards it has direct impact on those current questions of black hole physics.
The epicycle model, based on the geocentric theory of the universe (the earth is at the center of the universe), is totally capable of predicting the orbits of the planets and stars.
I don't agree with this. Far from being totally capable of these predictions, any actually existing epicycle model could only predict orbits up to the level of precision of the observations that went into that model. The Newtonian theory, besides having all of the good points that you identify, is also superior on the purely phenomenological level of making predictions (and this much is already true with Kepler). There were few refinements to Newtonian models before the advent of Einstein's theory, and each one led to the successful prediction of the existence of a physical object that could also be observed in completely different ways (such as by sighting the reflection of sunlight off of it). Refinements to epicycle models did not do this.
The modified aether theory is perfectly able to predict everything special relativity does. There’s no way to discriminate it from special relativity.
This I agree with. But here, the superiority of special relativity is perfectly clear from a purely mathematical standpoint. The aether theory features a quantity, the reference frame of the aether, that is necessarily unobservable; special relativity lacks this and is much more elegant. Sure, it is superior for the other reasons that you mention, but mathematics alone can also identify it as better.
Surely, [epicycle models] have many interesting geometric things inside, and a rigorous (and complicated) formulation of it could have led to big mathematical breakthroughs. Yet, how could such study helped to find Newton’s laws? From a physical perspective, all this work would have been totally useless.
Epicycles are of no interest mathematically; they are completely ad hoc. (Similarly, the precise layout of the planets and large nearby planetoids in our solar system, which refine Newtonian models, are of no interest mathematically; of course, Kepler tried to relate them to the Platonic solids, but this didn't pan out.)
But now imagine a world without Copernicus and Kepler, but with Brahe and Galileo; in this world, Brahe uses his own data to develop highly sophisticated geocentric models, and Galileo discovers the mathematical regularity underlying these models. Only at this point, where we have a law to predict more and more precise epicycles, can a geocentric model actually match the predictive capabilities of our world's heliocentric models. But at this point, we can also observe the superiority of the heliocentric models from a purely mathematical perspective. We only await the stroke of insight (perhaps due to Galileo himself) that suggests this mathematical simplification, and the history of science rejoins our world. (Newton follows, and so on.)
This never really happened. Even with special relativity, this is not how it happened (despite the work of people like Poincaré who arguably could have done it this way). But with general relativity, it did —not by Einstein but by Hilbert, at about the same time. So it can be done.
I don't think that anybody is happy with QFT, or even string theory, as we have it now. But research into its mathematical structure could well lead to the discovery of the same sort of insight. Arguably, it already has, but we have to work out the consequences of this new mathematical framework to be sure that it's right.
Thanks, Toby. I didn’t react to the “all this math looks epicyclically complicated” in the above, since I thought we should first try to clarify what it does, before we enter discussion of whether it’s beautiful.
Of course as regulars here are all too tired to hear me repeat, part of the point I like to advertrize is that the math is actually shockingly elegant, simple, and far less epicyclic than traditional formulations.
It often happens that people mistake “simple/easy/elegant” for “familiar” and “complicated/epicyclic” for “unfamiliar”. I once illustrated it this way: most people on the street will think they perfectly understand how gravity works while they think the inner working of a nuclear reactor is complicated. But what they really mean is that they are very familiar with stuff dropping to the ground and very unfamiliar with nuclear dynamics; while on absolute grounds, scientifically, fundamentally understanding nuclear dynamics turns out to be actually simpler than fundamentally understanding gravity.
Something like this is happening here: the derivation of classical field theory and at least good bits of quantum field theory from just homotopy type theory with some axioms added is fundamentally much simpler than anything traditionally done, but of course it looks more unfamiliar at the moment.
Hey “sure”,
I still don’t see that we are communicating.
Not sure how to usefully continue this exchange. If you do want some answer from me (maybe you don’t) I suggest to focus on one concrete aspect, for currently i see too many things being mixed up in too random a fashion.
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