On October 15, 2025, Sourav Chatterjiee gave the second of the Millenium prize lectures. I have started a page on this here where the slides are included.
A bit of nostalgia
Some of my own course assistants (when I was an undergrad) or grad student colleagues (when I was a grad student) worked on constructive quantum field theory and not all graduated. Pierre-Alain Bovier or Felix finster are two success examples. There were others who researched for many years and did not get anywhere. Already in 1990 the steam was a bit missing in Euclidean constructive quantum field theory. Konrad Osterwalder himself turned more to administration, later would become Rector at ETHZ or work at the UNU. Other folks in mathematical physics (like my PhD dad Oscar Lanford has started in QFT but changed to dynamical systems) have moved on to greener pastures. If one looks at the student list of Arthur Wightman (also my academic grand dad) then many seem have have moved on to other topics. Having seen so many talented mathematicians getting stuck in this field, it might just be that the axiom systems (like Osterwalder Schrader) mightnot produce the desired theorems or that something essential is missing. For me as a mathematician, it is not only the success with matching experiments (which often can be done by just introducing parameters and do data fitting, in particular use perturbation expansions- an engineering approach), what is also valuable is that a theory produces interesting theorems and preferably simple beautiful theorems not just something a referee has to accept because the author is somebody important and the proof is 100 pages long. Quantum mechanics itself has motivated many interesting theorems in operator theory and spectral theory, even algebra and logic. Also relativity also has been very fruitful and produced again zillions of interesting problems in the calculus of variations or Riemannian geometry. Maybe what happens in nature is correlated with how many “beautiful theorems” one can prove in a frame work. Some comments:
- Functional integrals (link to a slide of Chatterijiee) make me (and many other mathematician) nervous. I like the probabilistic approach where you have the Wiener measure as this is rigorous. The functional integrals written down formally just are too “adventurous” for mathematicians – to say it politely. To put it directly: it might just be non-sense.
- As for the Maxwell equations (link to a slide of Chatterijiee) , it really is much easier to express them relativistically. The Maxwell equations are dF=0, d*F=0 implying the wave equation L F = 0, where L=dd^*+d* d. Gauge transformation are
.
- The Yang-Mills existence problem is mathematically not defined in this talk. Here is Chatterjiee’s slide about this. This is my main gripe with this Millenium problem. It is just not well defined yet. Also the original article of Witten and Jaffe does not convince (at least me personally) that this is a good problem. It is too political of a problem. When asking a problem, one needs to specify precisely the boundaries of what is acceptable to work in. It might well be that a completely different frame work can explain the experiments better.
- The mass gap problem is is not defined in the talk. What is the Markov process? What is the Hamiltonian? Is one free to make this up? One can make up quite general Hamiltonians with a Mass gap.
- Monte Carlo simulations of lattice gauge theories were fashion already many decades ago. It was for me something I could in principle understand as it produces interesting questions in probability theory. Take a network and a compact Lie group valued function on edges, then compute quantities. On a finite lattice, all the fields produce a nice probability space as it is a quotient of the product space of Haar measures. Now one can ask questions in probability theory like expectation values of quantities. One can make Monte-Carlo experiments. Unlike ill defined functional integrals it is all well defined. I was fascinated by it and even wrote an article in this area but in a more classical setting, where the existence of critical points are studied using the “anti-integrable limit”, which is just an application of the soft implicit function theorem.
- Balaban’s work that has been mentioned in the talk was already fashion when I was a student. Here is one of the papers he wrote here at Harvard in 1987. I myself can not read this. It seems that many others have similar difficulties. I only can suspect that even the referees of such papers must have had difficulties to judge it.
- My perception has not changed that this field of mathematical physics has become too technical to be interesting (as for now). What was new to me from the talk that the problem has morphed to a problem in probability theory. There, one has a chance to prove theorems. Whether it really produces some insight when time is rotated is not clear.
- My own experience is that Wick rotation really does not seem to help much to gain insight into physics. It is a technical tool to make things converge. Analytic continuation can be a tricky business. Who knows what singularities lurk in the complex time plane.. For me it can make perfect sense to use the analytic continuation of the Riemann zeta function to make sense of the determinant of the Laplacian of the circle. However, it is not trivial to prove that an analytic continuation is possible for general manifolds. Has Wick rotation anytime really produced some insight?
