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An author has proven an interesting mathematical result, but notices that this result contradicts existing literature.
Does the author have to find an explicit error or counter-example to the existing literature before considering submission? Can she submit the proven result to a journal, if she cannot find an error in her own proof?
Certainly the fact that there is a contradiction with previous literature must be prominently advertised; to do otherwise would be scientific misconduct. I would not be confident in publishing such a paper unless I found the mistake in the other paper, or could give a counterexample showing they are wrong.
After having carefully worked out the other paper and my own paper, and asked any experts with whom I have an established connection, I might contact the authors of the contradicting paper (if they are still active). After their response, or lack thereof, I would consider publishing a preprint and after that submitting to a journal. The journal is the slowest and most uncertain way of finding out where the problem is.
Forgetting the issue of publication, when two mathematicians find contradictory results, I think they have the collective intellectual duty to try to figure out what is going on. Generally this should mean that one of the purported proofs is wrong; however, it could also be that an even earlier result (used by one or the other contradictory proofs) was incorrect; conceivably, it could even mean that a contradiction has been found in whatever foundations of mathematics were being used, but we probably shouldn't take this possibility too seriously.
Generally speaking, I would say the burden of figuring out the root of the problem lies with the author of the most recent result (were it only because the others of the other result might be retired or dead). So you can't just go ahead and say "I proved not-X" when X appears in the literature, you need to analyse why and where the proof of X is wrong.
There are exceptions, however. One extreme example would be that if you can find a numerical counterexample to Fermat's Last Theorem (that anybody can check with a computer), you don't need to explain where Wiles's proof was wrong (or even understand it). More generally, if your proof of not-X is conceptually much simpler and/or much shorter than the proof of X found in the literature, I would say that this is a valid reason to shift the burden of finding an error to the authors of the latter.
One valid reason (at least, valid from the point of view of intellectual honesty: it might be another matter to actually convince anyone) not to analyse the proof of X for error is if you don't understand the techniques used therein. If they are too complicated, this might fall under the "your proof is much more simple" category mentioned above. But a genuinely problematic situation might arise if two mathematicians from completely different domains were to prove contradictory results, neither being able to understand the intricacies of the other's proof; third parties would then need to get involved to resolve the contradiction.
But in any case, any contradictory result you are aware of should be explicitly mentioned in a publication, and whatever reason you have not to analyse their proof in search of the error should be explained.
Let me just note that Voevodsky (2002 Fields Medal) describes such a situation that he experienced himself (http://www.math.ias.edu/~vladimir/Site3/Univalent_Foundations_files/2014_IAS.pdf):
In October, 1998, Carlos Simpson submitted to the arXiv preprint server a paper called “Homotopy types of strict 3-groupoids”. It claimed to provide an argument that implied that the main result of the “∞-groupoids” paper, which M. Kapranov and I had published in 1989, can not be true. However, Kapranov and I had considered a similar critique ourselves and had convinced each other that it did not apply. I was sure that we were right until the Fall of 2013 (!!). I can see two factors that contributed to this outrageous situation:
- Simpson claimed to have constructed a counterexample, but he was not able to show where in our paper the mistake was. Because of this, it was not clear whether we made a mistake somewhere in our paper or he made a mistake somewhere in his counterexample.
- Mathematical research currently relies on a complex system of mutual trust based on reputations. By the time Simpson’s paper appeared, both Kapranov and I had strong reputations. Simpson’s paper created doubts in our result, which led to it being unused by other researchers, but no one came forward and challenged us on it.
EDIT (01/01/2018): Let me add another (IMHO, relevant and interesting) example. Asher Peres wrote (https://arxiv.org/abs/quant-ph/0205076):
" Early in 1981, the editor of Foundations of Physics asked me to be a referee for a manuscript by Nick Herbert, with title “FLASH —A superluminal communicator based upon a new kind of measurement.” It was obvious to me that the paper could not be correct, because it violated the special theory of relativity. However I was sure this was also obvious to the author. Anyway, nothing in the argument had any relation to relativity, so that the error had to be elsewhere...
I recommended to the editor of Foundations of Physics that this paper be published [5]. I wrote that it was obviously wrong, but I expected that it would elicit considerable interest and that finding the error would lead to significant progress in our understanding of physics. Soon afterwards, Wootters and Zurek [1] and Dieks [2] published, almost simultaneously, their versions of the no-cloning theorem...
There was another referee, GianCarlo Ghirardi, who recommended to reject Herbert’s paper. His anonymous referee’s report contained an argument which was a special case of the theorem in references [1, 2]. Perhaps Ghirardi thought that his objections were so obvious that they did not deserve to be published in the form of an article (he did publish them the following year [7])."
As a reviewer, I would definitely recommend rejecting such a paper.
I can certainly imagine that there will be such cases where there is an interesting conversation in the community to be held. However, this conversation does not need to happen via journal articles. The appropriate course of action would be to first discuss such a situation with a few experts. If none of them can resolve the situation, post the article on the arXiv and draw attention to via conference presentations, etc.
If an apparent contradiction receives significant attention and yet is not resolved, then publishing an article describing the conundrum might make sense. This article would be very different from the one described by the OP though.
To publish a contradictory result (in maths, as opposed to natural science) without further explanation would be to say "there is an error in one of these proofs but I don't know in which". Unless the issue at stake is of very great importance that is probably not a statement that is interesting enough to publish. I would say you should be able to point out an error, a counter-example or a hidden assumption in the original work.
Where there is no straight-forward mistake in either proof a hidden assumption should be considered possible and may be of real importance. An example is Von Neumann's purported proof that the results of quantum mechanics could not be produced by a hidden variable theory. This was contradicted by the development by Bohm of his pilot wave theory (a hidden variable theory that does just that). It was then realised that Von Neumann's proof, while not containing an explicit error, applied only to local hidden variable theories, and the pilot wave theory is non-local. This is an important distinction that (whether Von Neumann himself understood it or not) had not been generally appreciated.
This was a case of a physical theory providing a counter-example to a mathematical result about physical theories, thereby revealing a hidden assumption.
In pure mathematics it would be very unusual to publish a contradictory result with no attempt to resolve the paradox. Even in the rare instance you are suggesting the axiomatic basis of the field may need to be revised, you would be expected to have an opinion on the correct resolution. (The history of set theory provides examples of this type).
https://en.wikipedia.org/wiki/Hidden_variable_theory#Bohm.27s_hidden_variable_theory
https://en.wikipedia.org/wiki/John_von_Neumann#Mathematical_formulation_of_quantum_mechanics
We had a similar situation once we were trying to solve an interesting problem in Thermodynamics of interfaces. While all earlier reports claimed a specific quantity to be always negative, we consistently received a positive value.
We were skeptical and began to look critically at our work and also the earlier works. Such a situation in principle says something new is found which contradicts other. Most of the times you have to place your scientific arguments not just by stating why you are correct but also by at least speculation why others could have been wrong. (Please, keep in mind that others were well-renowned scientists who did good science. But we all make mistakes and most often correct them).
Why is it good to speculate what could be wrong in literature?
Provides a stronger proof and explicitly claims other people are wrong.
Shows authors knowledge that he had understood others work before he claims something about it. Particularly helpful if your speculations are more logical and scientifically sound. Even a marginally acceptable argument, if valid, is sufficient enough to convince referees and readers.
Attracts more readers, often speculating other works requires citing them. Having cross-reference to earlier works is hugely a good practice. Attracts also the scientists whose theory you refute.
By the way, in our work, we were happy to find a flaw in literature. We are now planning to prove our theory using multiple methods (theory, simulation, and experiment) before we begin writing about it. (That is why I do not provide details in this answer)
Been there, done that.
During my MSc thesis I found that some (quite perplex and rare) thing from a book did not work as described there. (To be fair, the book definitions were not wrong, but ambiguous, however, the examples clearly showed the intended approach.) The way I did it (slightly, but decisively different), it worked. I was very cautious (being a student) in formulating the thesis. But it worked out and I got my best grade on it.
Putting the careful formulations aside, the thesis was like "they try to do XYZ in a abc way. It fails, here is a counterexample. If you change XYZ to XYZT, it works, have a look." In my eyes it was and still is a rock-solid research result. That's how science is made.
PS: Oh, and this happened in Germany, so a MSc is not a sign of a failed PhD, but rather the standard degree.
Sometimes, on further examination of the contradiction, one finds that both cases are true but that these cases are subtly different. The von Neumann proof above is an example. A trivial (formal because I don't remember an actual) example would if one result used an axiom system "A" with a seemingly simple extension "y" and the other used system "A" with the seeming equivalent extension "z" so that A+x gives results different from A+y whereas x and y may yield the same results if using B in stead of A.
This is probably covered above in the post about some not so obvious result used by both papers being questionable.
TL/DR: Peer reviewed literature is not doctrine. That a result contradicts "accepted truth" does not mean that it should not be published. All that matters is that the result be properly checked for errors. If there are no apparent errors, then let the academic community decide why there are two seemingly correct yet conflicting results.
If you find a result that contradicts existing thought, publish it. Whether or not a result contradicts standing thought should not affect its acceptance or rejection. Only the quality of the argument should have an impact. I say "should not" because it is sadly not always the case.
If you are not certain as to whether or not your conclusion is correct, find someone with whom you could discuss the matter and see if they agree. If you can find someone prominent with whom you can co-publish, and who can add to the argument to make it more robust, then you might want to look into that.
Automatically Wrong
There seems to be a bit of a suggestion that if it contradicts existing literature, it must be wrong. Now, I suppose in mathematics, it is usually relatively "simple" to verify a proof, but even then there can be errors. Make sure you know what you're talking about. Get some feedback. But do not assume that you are wrong because the current literature is against you. If this contradiction were in science rather than mathematics, even more the reason to not assume that you must be wrong.
Much of published literature, at least in science, overrides past literature. In science, we only assume that a theory is true, until we find evidence which contradicts it (Further discussion on the nature of science). Mathematical theory can be such evidence.
Again, if your thesis is well thought out, properly explained, and an expert in the field cannot find an error with your work, there is no reason to assume that your answer is wrong. Just because an existing answer is accepted by academia should not dissuade you.
Conflict Resolution
There has been a suggestion that before publishing the paper, it should be determined which position is correct. However, that might not be possible, or neither party may have an answer. Publishing a result, so long as it is not apparently flawed, allows the community of experts to become aware of the potential alternative and work on explaining the conflict. As a professor recently said, the main way in which experts in a field communicate is through peer review. To refrain from publishing because the question of whose position is correct has not been resolved would in some ways be withholding potentially useful information from the academic community.
Doctrine
David Richerby made an interesting case. He suggested that because the other theorem has already been accepted, it should now take additional effort to overturn it. However, there is nothing that seems to be wrong with either theorem (at least according to the OP). David's suggestion means that if the OP's proof were conceived and received first, and it were the other result that was later identified, somehow the burden of proof would switch and now it would require exceptional levels of justification to get that result published. In other words, the order in which the result was produced is the only thing that is changing, and yet somehow that change takes the OP's result from requiring extraordinary proof to requiring ordinary proof and takes the currently established result and demands that now it would need extraordinary proof.
When a result carries more weight, simply because it is already established as being "true" by a group of people, that result becomes doctrine. That is not how academia works. That is not how research works. The validity of a result, and the level of justification needed, is determined only by the result. So long as there are no apparent flaws, and the result has been reasonably checked for flaws, as all results for publication need to be, then the answer is obvious: publish and let the academic community work on resolving the conflict.
Dan Fox linked to a very interesting example. "In 1991, Kapranov and Voevodsky published a proof of a now famously false result." In 1998, someone came up with a contradictory result, but could not find the error in the original proof. Ignoring what would have been the apparent consensus advice of SE Academia, the result was published anyway. It was not until 2013 that an error was found in the original proof, and it might have taken a lot longer had Simpson not pushed the issue by publishing his own result.
