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Two kinds of papers. There are two kinds of papers: self-contained ones, and those relying on published results (which I believe are the vast majority).

Checking the result. Of course, one should check carefully other's results before using them. There are several incentives to do that: become a real specialist; expand one's knowledge of concepts and techniques; find and mention a gap in the proof should that happen; get the ability to interact with more people ("I read your paper..."). So ideally, in a sense, checking a result before using it should always be the case.

Trusting peer-review. Yet, the very idea of academic peer-reviewed publications is to allow readers to locate results deemed trustable. The implied degree of trustability varies among scientific disciplines, but one would expect mathematics to have to most stringent one: a proof is either correct or it is not.

Given this, it is sometimes very tempting to use a result as a kind of "useful axiom", especially if that result has been proven with concepts very far from one's own area(s) of expertise, or if it is the culmination of several long papers: in those cases it would require a substantial amount of time, maybe even years, to personally check the results in their own right. Someone wanting to move forward quickly (or with a short-term position) may not want to go into this.

How to decide? Some cases are clear-cut (e.g. most people would accept the classification of finite simple groups), while others are borderline.

My questions on that matter are:

  1. Are there rules of thumb that you have come up with when deciding between checking a result, and taking it as an axiom ?
  2. When accepting without checking, how do you phrase it?
  3. Has it ever occured to you that taking a result for granted actually backfired: what happened, and what would you do differently (job interview, retraction of publication)?

EDIT (friday 7 may): many thanks to those who have replied, very interesting comments! (Also, please note that since there is no "best answer" to that kind of question I will not single out one over the others.)

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It's not clear that peer review is meant to imply that published results are trustable. One possibly reasonably interpretation is that published papers have some threshhold probability of correctness. Thus peer review doesn't save you from needing to check results; it merely saves you the time to avoid checking the stuff that is most likely to be wrong. I'm not endorsing this viewpoint, but it's worth keeping in mind that some referees may be acting with this in mind. –  Mark Meckes May 6 '10 at 18:29
Perhaps I should mention the personal experience that makes me say this: I once got a (positive) referee report in which the referee said that he or she had "sampled some of the proofs" in the paper and found them to be correct. –  Mark Meckes May 6 '10 at 18:30
@Mark: Your referee was more honest than most. Having been involved in refereeing hundreds of papers over many decades, I know how demanding the job can be. Editors usually make it clear that the referee is not responsible for the correctness of a proof but should make a reasonable effort to evaluate it. –  Jim Humphreys May 6 '10 at 18:49
@Jim: True enough. I wouldn't completely vouch for the correctness of every detail in all the papers I've refereed, either. What struck me was the implication that this referee had completely ignored some of the proofs (and it wasn't a long paper). –  Mark Meckes May 6 '10 at 18:54
I believe the instructions to referees from the AMS say explicitly that the responsibility for correctness rests with the author rather than the referee... –  Gerald Edgar May 7 '10 at 15:19
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8 Answers

In a word: never.

But slightly more usefully, here's my 50øre. If you publish a paper that depends on the result, are you going to be embarrassed if the referee says, "Can you clarify your use of Theorem X?". If you feel happy saying, "A,B, and C all published result depending on it, so I figured I was safe." then go ahead. If you're not quite so sure that A, B, or C check things quite so carefully as you do, check it yourself.

So, for example, if it's a result about differential topology on loop spaces then I would check it very carefully because I ought to know about that stuff and I would be embarrassed if the referee said that. But, say, Kuiper's result on the contractibility of the general linear group, then I figure it's not quite my area of expertise and plenty of other people have used that result in the meantime that if someone finds a mistake now then my minor embarrassment is going to vanish into nothingness besides the other things that are going to come crashing down.

To put it a slightly different way, suppose that you prove X, which depends on Y. Then someone proves W depending on your X. Later, Y is found to be false. When you and the person who proved W happen to be at the same conference, do you a) hide in a corner and hope that they don't see you, or b) go to the pub and have a good laugh about it all. If you think it'll be (a), then you should have checked Y. If (b), then you're in the clear.

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Rather selfish point of view, but also extremely practical. Just to illustrate that mathematicians are people too (as opposed to some sort of Romantic tragic hero). –  Willie Wong May 7 '10 at 14:21
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There obviously won't be a single answer that fits all circumstances, but here is my pennyworth.

If a result is sufficiently accepted by experts you have good reason to trust, then the result can be trusted. (Obviously the better you understand it the better, but sometimes one has to save time.)

If a result does not satisfy the first criterion, then be very suspicious of it unless you are given, or can think of, some accompanying reason for its being true (rather than a long calculation that just happens to work).

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Here is a rule of thumb I learnt the hard way: if the article A you are using seems to be under-quoted, that is to say if articles published later quote other sources while A seems to be perfectly acceptable, then beware of A.

Suggesting this rule of thumb pains me greatly because I think there are already too much path and cultural dependancy in citation practices in mathematics. That is I think the importance of some authors and/or works are downplayed and underestimated because people tend to quote the version of a result they learnt first in their mathematical education, or the one published by someone they know, or the version they actually read in details instead of the one with historical and/or mathematical precedence. And yet here I am suggesting one should beware of rarely quoted papers.

But the truth is, even though I could still be considered a relatively young mathematician, I already maintain a quite long list of serious mistakes in articles with impeccable pedigree (excellent journals, ICM class authors...) so I suspect everyone does the same. The problem is that upon this subject, everyone (including me) seems to operate on an "everyone knows" basis.

So everyone (in my field) knows that Deligne's Travaux de Shimura (EDIT: actually in Deligne's article in the Corvallis volume, as pointed out in comment by the person who found and corrected the mistake in the first place) contains a sign mistake, everyone knows that Bloch-Kato's article on Tamagawa numbers contain a recurring misprint (except Dummigan, Stein and Watkins sweat to prove a lemma apparently because they didn't know about it), everyone knows that Skinner-Wiles on residually reducible representations contains a mistake (except I agonized over it several weeks before asking a senior member of my department who immediately replied, "yes, everyone knows about it") etc.

So if an article is underquoted, it might be because "everyone" knows that there is a problem with it, so maybe it is a good idea to double or triple check in that case. Watch it especially if the authors themselves seem to have "forgotten" about their own paper (in that case "everyone knows" might mean "the authors know").

As you gathered, I have made mistakes because I took for granted a published result. So my answer to your number 3 is: in that particular case, nothing spectacular happened, I was the only one to notice my own mistake (the referees missed it), I alerted colleagues and friends whom I knew had used the same result or intended to quote my work and put a sentence in my next article saying that one had to put an extra hypothesis in my previous work on the subject because an extra hypothesis was required in one of the sources.

EDIT: Reading comments, I realize that my answer could be read as meaning that I actually think that everyone knows the mistakes I mention, and hence support the "everyone knows" attitude. This was meant as irony, pointing out to the fact that in reality, very few people know about such mistakes (in my experience), and that many people (me included) have sweat for weeks only to discover that some people thought this was so well-known as to be self-evident. I apologize for the ambiguous statement and record that my position is that this "everyone knows the mistakes in other articles" actually produces the result "someone, somewhere noticed the mistake for a few weeks" and "generation of researchers will reproduce the mistake or lose time trying to figure out what went wrong".

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Actually, the signs in Deligne's Travaux de Shimura are correct. It's in his Corvallis article that he got them wrong... –  JS Milne May 7 '10 at 12:50
Making a mistake in a list about notorious mistakes! Ah, the irony! Thanks a lot for the correction. –  Olivier May 7 '10 at 13:49
@Olivier: I find the "everyone knows" mentality about errors in published work annoying and sometimes infuriating. At first glance, you seemed to be supporting it. Reading your response carefully, I found that you have justified my sentiments quite well: i.e., the problem with "everyone knows" is that too often, manifestly not everyone knows. Thanks for your answer. –  Pete L. Clark May 7 '10 at 14:49
@Pete: I am happy that I am not the only one annoyed. It is great time that with the electronic availability of most mathematical articles, a common open sourced technology of maintaining errata together with the soft copy of the original article and good search engine for the greater good of the mathematical community be established and of widespread use. So that people saying "everyone knows this error is there" would be ashamed not to have checked if this errata entry had been entered and would be even more ashamed of not having entered it him/herself. –  ogerard May 7 '10 at 16:03
Maybe I am naive, but why not publish an erratum? –  Boris Bukh Feb 21 '11 at 13:55
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No-one has quite answered:

  • When accepting without checking, how do you phrase it?

I think? So, here's a thought. I'm always of the opinion that you should give the maximal amount of detail where referencing something. Give the exact Theorem number in the paper you reference (not just ``by results of [12] it follows that...''). Explain carefully the hypotheses and conclusions. Of course, the more accepted a result is, the less detail you need to give.

If, however, you actually want to reference the proof then I'd be very careful. E.g. you might observe that the paper shows X=>Y, but the proof works for the weaker X'. I'd be tempted to give a sketch, or outline exactly the changes needed.

My guess is that a lot of subtle errors can be introduced by referencing proofs: I've heard it said that most mathematical results are true, but many proofs are subtly wrong. So it might be true that the proof in [12] shows that X'=>Y, but maybe the author stated it only for X because there is a subtle error in the proof, and really the stronger X is required. (This, of course, is also a good test of your own proofs, but I'm heading off topic...)

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Excellent advice. Detailed references are much more helpful to the reader. And I have seen serious gaps result from referencing proofs. –  Nate Eldredge May 7 '10 at 15:15
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This question was discussed on E. Kowalski's blog.

Here is a comment I made:

Dear Emmanuel,

You have raised an interesting issue, with (I believe) no simple answer. I think that Terry’s suggestion on how to deal with the situation is a sensible one. I might add another piece of advice. (Note that, as with Terry’s advice, this is not advice on how to address this issue in one’s writing, but rather, how one should proceed when confronted with this situation in one’s research, so as to avoid blunders.)

Most pieces of mathematics (including Weil II, for example) fit into a framework (and I don’t here mean a logical framework, but rather a narrative framework), with illustrative analogies to other parts of mathematics (in the case of the Weil conjectures, there are important analogies with algebraic topology and Hodge theory), interconnections between various results in the area, key motivations and heuristics, and so on, and one can often learn these even if learning the actual details of the arguments is out of the question.

If there is such a narrative that one can learn, I would say it is normally a good idea to learn it, since it will give one a better feeling for the results being cited, and a better feeling for how to apply them correctly. On the other hand, if such a narrative structure isn’t available, it will probably be harder to test the correctness of one’s understanding of the results, since (short of actually reading the proof), there is nothing to check against. Perhaps in such a situation, it is probably a good idea, if possible, to verify with an expert that one is really applying the result in a correct manner. Good expository literature can also help a lot (both to learn the narrative, if one is available, or at least to learn one’s way around the results that one wants to apply).

On the question of how one should phrase the citation in such a situation (of citing a result whose proof one doesn’t know): I think that having a good understanding of how to apply a result is itself a valid and important skill, whether or not one knows how to prove the result. (Similarly, we value good drivers/pilots of vehicles, as well as the engineers who build the vehicles themselves.) I don’t think that there is any intellectual dishonesty in citing a result with confidence, if one is genuinely confident that it is true (and trust in a group of established experts is a genuine and legitimate source of confidence) and one is genuinely confident that one understands the statement and the ways in which it can be applied.

On the other hand, if one doesn’t have this genuine confidence with regard to a result that one is applying in some argument, then one could be heading for a blunder, and I would say that caution is required, not just in the citation, but in the construction of the argument itself.

Just to add to this: if a result is generally certified by experts, is well-established, and widely used and understood (even if not by you personally), then there is surely no problem in quoting it, applying it, and relying on it. (As Andrew notes in his answer, if such a result does somehow collapse in the future, you will have plenty of good company with whom to commiserate about the collapse of you own work.)

On the other hand, if a result is not like this, you should be more cautious in applying it, not for any ethical reason (at least in my view), but so as to avoid having your own work built on an unstable foundation. As I write above, when you can't verify the result yourself, do your best at least to see that it fits into a reasonable narrative framework, and also try to find experts that you trust who can certify the results correctness, and that you are applying it correctly.

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The questions raised are real but can't be answered by giving rules of thumb, I'm afraid. Mathematics is hierarchical by nature and has a long history, with results often building on earlier ones. Peer review of published work varies a lot in thoroughness, but even done conscientiously can't root out all subtle errors. Most of us bring a bit of skepticism to results we haven't understood deeply on our own. Many of us publish results which are not quite right (making later corrections when feasible). It's always risky to quote stuff at random from areas you are not a specialist in, even if you trust the people involved. If you are a specialist, you probably trust some people more than others to get it right; but even so you try to check details. A great many mathematics papers contain at least minor errors, in most cases correctable but not self-correcting. Some real mistakes become famous and spawn important research.

You write: How to decide? Some cases are clear-cut (e.g. most people would accept the classification of finite simple groups), while others are borderline.

Actually, most people I know accept the classification only conditionally, as do some of the real experts in the subject who are still working to codify a complete proof. A result like this, plausible as it looks, depends on a huge amount of published (and some unpublished) work. I think it's still customary to point out in papers when the CFSG is being used to get other results.

If you have to quote results you haven't understood from scratch, you should try to access the MathSciNet database in order to read a review and follow up later citations. Or try to ask an expert. Lacking that, quote at your own risk and without offering too firm an endorsement, e.g., "Theorem X in paper Y states that Z".

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P. Halmos in "I want to be a mathematicien" has a short section on refereeing where he exposes his point view: The role of the referee in his eyes is not to certify correctness of a paper (this is the authors job, according to Halmos) but he has to "smell" a paper and to advise the editors on its interest (I am citing from memory and hope that there is not too much distorsion).

As a referee, I am following his advice in the following sense: If I enjoy reading a paper then I recommend it generally for publication (and in this case I check also more or less carefully the proofs). If I can find no pleasure and no interest then I suggest either another referee if the paper seems interesting nevertheless or I recommend rejection. In the last case, I do generally not check proofs (and I tell the editor and the authors so).

In some sense, mathematics should mainly be interesting, errors in very interesting and stimulating papers can be tolerated to some extend since they will generally get quickly corrected. (This is of course only true for exceptional papers, most papers have close to zero readers anyway.)

Mathoverflow is somehow a mirror of the mathematical litterature (except that the process is much faster on MO): Erroneous statements get quickly commented and eventually corrected or retracted.

I believe that the possibility of making errors is a necessary part of any creative process. Computers make (generally) no errors. They are also more stupid than the most disabled human who is not braindead.

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It is the life's work of many people to make this question obsolete. More precisely, we aim to make mathematical assistants which are both pervasive and easy-to-use so that, in say 50 year's time, all high-quality journals would immediately reject a paper which has not been checked by one of these systems. [There are sub-fields of computer science where the time horizon for this seems closer to 5 years, with the 'best' papers already being machine-checked today].

Note that some people mis-interpret such statements. In the past, it is true that formal verification was extremely difficult and it intruded too much into the actual results and their write-up. But this has changed tremendously of late, where 'modern' verified papers (through the liberal use of literate programming tools and ideas) look the same as non-verified papers, they just come with attachments which contain the fully formal parts. Mathematical papers can then retain their human-oriented aspects of communicating the crucial ideas and insights, while allowing a certain lightening of the formalism in the text.

This is coming. Current mid-career mathematicians don't have to worry about this too much, but I would certainly advise the younger generation to keep an eye on these developments.

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I'm a bit skeptical about this. It might work in some algebraic areas, but in (nonalgebraic) geometry I can't imagine this happening. It's already hard enough to write a paper which is based on subtle geometric or visual reasoning without the burden of trying to formalize everything. The subject would never progress! And in the end, there are so many subtle places where the formalization can go astray that I don't think it would add much. –  Andy Putman May 10 '10 at 15:18
@Andy: our ultimate goal is to make it a benefit (relieving mathematicians of tedium) rather than a burden (ie, imposing it). Even in geometry, I think in some cases it will be essential. For example, Hales' reviewers were simply unable to fully confirm his claimed proof of the Kepler conjecture, despite running a three year seminar on it. His project to mechanize his proof seems to be the only sensible response to this state of affairs. –  Neel Krishnaswami May 10 '10 at 21:26
@Neel: we are in complete agreement. –  Jacques Carette May 11 '10 at 7:36
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