# Are there mistakes in the proof of FLT?

This semester, I teach a graduate course in epistemology of mathematics and as a case study, I assigned students a discussion on the epistemological status of Fermat's Last Theorem according to different epistemological point of views. One of the hard-line stances we discussed in the course was the one which considers an assertion as being a mathematical theorem only if it comes with a completely rigorous proof.

In 1990 and 1995, the papers On modular representations of $$\operatorname{Gal}(\bar{\mathbb Q}/\mathbb Q)$$ arising from modular forms, Modular elliptic curves and Fermat's Last Theorem and Ring-theoretic properties of certain Hecke algebras by K.Ribet, A.Wiles and R.Taylor and A.Wiles respectively were published. Presupposing previous mathematical knowledge, they form a complete proof of Fermat's Last Theorem.

My question is the following:

Are there any mistakes in these 3 papers of some mathematical significance?

Of course, it might be hard ot judge what is of significance, so let me mention a couple of things which I believe are not significant.

• Typographical errors are not significant, even if they alter the mathematical content (so if it is written $$r\leq s$$ while the proof shows $$s\leq r$$, that is not significant).
• Reference mistakes are not significant (so if there is a sentence like "by lemma 12.8 of [6], we conclude" and lemma 12.8 of [6] allows no such conclusion, but it is easy to see that lemma 4.2 of [11] would do equally well, then that is not significant).
• For the same reason, I will not count an easily filled incomplete argument as significant, even if strictly faulty (so for instance if there is a sentence like "X is a cosy zip, and every cosy zip is a zap, therefore X is a zap" and in fact it is not true that every cosy zip is a zap, but it is true and equally well-known that every strongly cosy zip is a zap and it easy to check that X is a strongly cosy zip, I won't consider this significant).

I would count as significant anything that requires more than a few sentences of essentially novel content (compared to the content provided). If for instance, it is claimed that a certain $$x$$ can be of 3 different types, each of which satisfy property P, so $$x$$ satisfies P, but it turns out that $$x$$ can be of a fourth type. Then, I would count this as a significant mistake even if $$x$$ satisfies P in this fourth case as well, but for reasons different from the first three cases. In particular, an error does not need to threaten the complete proof nor even the local part it is contained in to be considered significant.

Basically, I'm thinking of a standard much below what formal certification of the proof would require, but still quite stringent. I think that most authors and referees typically do not achieve that standard in most published papers, though some regularly do even in proofs of deep and hard theorems (I think it is believed that Serre achieved it throughout his career with very few exceptions).

With such a standard, are there known mistakes in these 3 papers?

• Why only these three papers? Langlands on cyclic base change and Mazur on the Eisenstein ideal are in particular both very difficult "previous mathematical knowledge" needed to absorb the FLT result. See also Kevin Buzzard's view: xenaproject.wordpress.com/2019/09/27/… Nov 19 at 16:01
• @Olivier - After looking at the various answers and questions you've posted on MO, I gather that your area of expertise is very close to these papers. How about emailing the authors and asking them directly? Also, there are many discussions of the problems Wiles had along the way to the proof - why not use those? Nov 19 at 16:05
• I'd suggest that for your purposes, Perelman's proof of the Poincare conjecture is a better case study. The consensus is that Perelman's papers are correct and that he deserves full credit for Poincare. On the other hand, filling in the details was highly nontrivial. Note also that Kleiner and Lott have said that Perelman's papers "contain some incorrect statements and incomplete arguments." But they "did not find any serious problems, meaning problems that cannot be corrected using the methods introduced by Perelman." See also this MO question. Nov 19 at 16:09
• Re-reading your answer, I see that it may be too late to offer alternative suggestions, but if it's not too late, you could also consider the classification of finite simple groups or the revision of the proof of the Kepler conjecture. Nov 19 at 16:22
• @Olivier I see. So maybe something like Manin's proof of the Mordell conjecture over function fields might qualify? Coleman (Enseign. Math. 1990) found and fixed a gap. "In the process of translating Manin's proof of Mordell's conjecture over function fields into modern language we found a gap. ... I believe all this is testimony to the power and depth of Manin's intuition. ... Manin has kindly verified that the corrections discussed herein are necessary and apt (see letter to Izvestia...)" This wasn't controversial at all as far as I know. Nov 19 at 18:03

No there are not any mistakes in these papers of any interest. In the 1990s there were a bazillion study groups and seminars across the world devoted to these papers; I personally read all three of the papers you cite, back in the days when I was young and an expert in this area, and they all looked fine to me, and they all looked fine to all the people who were at the IAS with me in 1995 reading them including a whole bunch of people who were a whole lot smarter than me.

As has been pointed out the proof of FLT relies on a whole lot more stuff than just those papers, for example Langlands--Tunnell (which I have not read, and suspect I will never read, but which has been generalised out the park by other authors) and Mazur (which I read through once but which others have read through many many times; it's the kind of paper that some people get addicted to and spend many years devoted to). The full Wiles paper uses Deligne's construction of Galois representations associated to higher weight modular forms, because it proves more than FLT (e.g. it proves R=T for some Hida families) and I've also not read Deligne's construction, but I know people who I trust and who have (e.g. Brian Conrad).

Some comments which might be of interest to you:

1. I was a post-doc in Berkeley in the mid-90s and during that time I read Ribet's paper; occasionally I would find stuff which I couldn't quite follow, so I would knock on Ken's door and ask him about it, and together we would figure out what he meant. A mathematician would not call these mistakes; one could argue that sometimes there were explanations omitted which you have to be an expert to reconstruct, but I think that this is true of many many papers. In particular a mathematician would not call these "mistakes".

2. Wiles uses Gross' results on companion forms, which at the time were not unconditionally proved; Gross' arguments assumed that two "canonically"-defined Hecke operators acting on "canonically" isomorphic cohomology groups coincided; at the time nobody had any doubt that this result was correct, but there was no published proof in the literature, and indeed it looked at the time that it might be hard to check. By 1995 Taylor had discovered a workaround which avoided Gross' work so the experts knew that there was not a problem here. The fact that the Hecke operators did actually coincide was ultimately verified by a student of Conrad in the early 2000s.

3. Wiles uses etale cohomology in some places, and at the time there was a lot of noise generated by logicians about whether this meant that he had assumed Grothendieck's universe axiom, which was known to be something which one could not prove within ZFC (indeed it was known to the logicians that in theory ZFC could be consistent but that ZFC+Grothendieck's universe axiom could be inconsistent). However Deligne's SGA4.5 had, years before the FLT proof, shown that the theory of etale cohomology could be developed within ZFC.

• Excellent answer. But let me ask this. The revision of the proof of the Kepler conjecture lists mistakes—a major one in Section 8, and lots of minor ones in Section 9 (page 35). If I understand Oliver correctly, he doesn't count the one-liners in Section 9, but he might count the longer entries (that take a paragraph or two). I gather that for FLT there is nothing as big as the gap of Section 8, but would any of the things you (as a postdoc) asked Ribet about be included in a meticulous list of errata, and require more than a single line? Nov 22 at 14:03
• Of course if we formalise the Wiles and TW papers I might have to revise my answer later :P It's probably also worth mentioning that by 1996 everyone was reading Darmon-Diamond-Taylor, which was a summary of the proof + refinements which had shown up shortly afterwards. And that paper has a false proof in ;-) I spotted the issue after the paper had gone to press. But it's OK! The experts know how to get around it. So that's alright then. Nov 22 at 21:59
• Probably also worth saying that if you'd asked me "is there a mistake in the proof of the Artin-Tate Lemma in Atiyah--Macdonald" then I would have said "no it's absolutely fine" but then one of my undergrads formalised it in Lean and this happened twitter.com/XenaProject/status/1308693991144206336 . So take everything I say about no errors with a pinch of salt! Humans are fallible! Nov 22 at 22:15
• The buzz from logicians was never "oh no, Wiles used inaccessible cardinals!", it was always "Oh, yes! Finally people just use inaccessible cardinals without fussing about them!!!! Woooo!!!!" Nov 23 at 10:54
• @AsafKaragila My take on it was that the debate was a linguistic one, centered on what it means to "use" an axiom. See this MO question for more details. Experts reading the proof of FLT could "see" that universes were irrelevant; less expert readers got worried when they saw citations of (e.g.) SGA4 as a black box. Nov 23 at 15:13