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I'm sure I'm not the only one with this quandary so hopefully this question is suitable for Mathoverflow. I'm posting anonymously for obvious reasons.

In a couple of my papers I have answered questions which were fairly well known inside my sub-field and posed by well known people. However, the solutions themselves are not hard - they do not involve any substantially new idea, other than perhaps the insight that some well-known techniques in a slightly different field could be of use. In the end I submitted (and published) to journals taking into account more the difficulty of the solution rather than the prestige of the problem. Several people later told me I could/should have aimed higher.

Now I am in a similar situation, with a couple of papers in preparation where the techniques I use are well-known, but they have just not been applied to the type of problems I solve (which again, are questions asked by very good people and open for at least a while. They are not major famous questions). Maybe I just have a good smell for low hanging fruit!

My concrete question is twofold:

  • Generally speaking, are papers who answer a respectable open question judged more for the problem solved than for the difficulty/innovation of the solution?
  • What are some good journals that welcome this sort of papers? (General journals as well as specialized ones)
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    $\begingroup$ One thing you can do is jazz up the intro and abstract to point out that you are for the first time applying technique X to field Y, and it fairly easily yields the solution to open problem Z. Thus the importance of the paper is not the difficulty of the proof, but the introduction of technique X. This sort of paper has the potential to be widely cited as other researchers in field Y start to use technique X, so I think a good journal is very appropriate. $\endgroup$
    – Jim Conant
    Commented Feb 22, 2012 at 14:01
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    $\begingroup$ Depending on the field, it is not unusual to have very important papers that are nevertheless very short and easy to follow. In that case, it's getting the right idea that counts, and if you're the first one to solve a long-standing problem, then people are not shy about giving you a lot of credit for your idea. But this might be related to field-specific culture, so you have to play it by ear. But as pointed out below, if you've been told to aim higher, you probably should. $\endgroup$
    – Thierry Zell
    Commented Feb 22, 2012 at 15:56
  • $\begingroup$ If it answers a problem that other people have posed and at least a few have tried seriously to solve, then an elementary solution is a testament to your ingenuity and IMO even stronger than a long difficult and technical paper; publish in the best journal appropriate to the question. If it answers an uninteresting question raised in passing in a little-known paper and you've never heard of anyone working in it, then consider it a much-needed gap in the literature and leave it alone. $\endgroup$
    – Gordon Royle
    Commented Feb 23, 2012 at 9:44
  • $\begingroup$ I agree with quid's answer (mathoverflow.net/a/89200/11540). If the problem was seriously attempted by others and then you solve it, that's a positive not a negative. But sometimes, the problem was considered "folklore" and the proof you wrote is one people might expect. Or, maybe there was already one proof in the literature and you found a second proof. In either case, consider submitting the paper to the Graduate Journal of Math (gradmath.org). Recording folklore and "alternative" proofs is a service, and can help grad students. $\endgroup$
    – David White
    Commented Apr 3 at 15:57

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I think you already have your answer: if you've been told to aim higher by several people who know your work better than we can, then aim higher :-)

More philosophically, it's a good idea to take an empirical approach to your own career. Don't make too many assumptions about what will or won't get published; instead, try out different strategies. In this case, you know that you can publish your results on lower-ranking journals. Now it's time to do the experiment where you try for higher-ranking ones.

As for which specific journals, why not ask the people who posed the problems to begin with? Or think about where you'd like to read this kind of result. On a more specific level, you might think about your introductory paragraphs, and what is the broadest possible audience to whom you'd be able to explain why your results (the results! not the proofs!) are interesting.

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Regarding (which it seems was so far not answered)

Generally speaking, are papers who answer a respectable open question judged more for the problem solved than for the difficulty/innovation of the solution?

In general, in my opinion and observation, more for the problem (by those that knew about the problem to beging with). If there are people that knew about the problem, perhaps even thought about it themselves, yet could not answer it, and now it is solved then this is remarkable. The following is a matter of taste, but one can (and I do) even find a 'simple' solution to a known problem more impressive than a 'complicated' one. If there is a 'simple' solution that sofar nobody found, than actually it was not at all 'simple' even if in hindsight it perhaps looks like this. Yet, a long complicated one, perhaps people even suspected it could work like this, but just did not do it out of some form of lazyness or fear of spending a lot of time and then it would not work. Also, a new simple proof of something known might be interesting, a new (more) complicated one rather not (exceot perhaps it comes along with some conceptual insight or surprising connection).

Yet, since you stress the subfield aspect, regarding the choice of the journal, it could be a good idea to submit it to some editor that is likely to have known about the problem. Or, at least to make in the introduction quite clear that what you are solving is a known problem around since a while. Otherwise you run the risk that this aspect is overlooked, and then it could/would be more about difficulty/innovation of the solution.

Regarding specific journals, I think the situation you describe is quite general, so that I would not know what to suggest based on this. Except perhaps: some journals have specific restrictions regarding the lengths of papers. So in case your papers should be short (say less than ten pages) and you should be
worried about this, you could (but don't have to) pick a journal with an upper bound on the lengths. The Proceedings of the AMS are one example, the Bulletin of the LMS another one.

Another general strategy (not always a feasible option) is to submit the solution to a problem to the/a place where the problem was raised.

Finally, I agree that asking people familiar with the situation and trying things out is good advice. And, a rejection of a paper is not the end of the world. So, if you do not need the acceptance/publication quickly, why not try to aim high, if ever the paper is 'thrown back at you' you still can aim lower later, while the converse is not possible. (Needless to say, one should not overdo this, as it causes work, and delay, for various people, but to try it on oaccasion seems certainly fine.)

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    $\begingroup$ Regarding submission to LMS journals. The process changed in 2011. Now you pick a journal based on the following bounds on page number: Proceedings, 22 or more; Journal, 15 to 28; Bulletin, 18 or less. $\endgroup$
    – Mark Grant
    Commented Feb 22, 2012 at 15:08
  • $\begingroup$ @Mark Grant: thank you for the correction. I had not yet noticed this recent change in process. I will remove the parenthetical remark and thereby correct the answer. $\endgroup$
    – user9072
    Commented Feb 22, 2012 at 15:13
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It should be mentioned that now the Annals of Mathematics want "short excellent papers", and they propose a quicker refereeing and publication process for paper below 20 pages to attract these.

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It may be that a mathematical method is fairly trivial but the idea of applying it to a particular problem in biology or astronomy or engineering or something would occur only to a genius. If that happens, then it would seem that a journal devoted to one of those subjects is the best place for it.

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If the paper is easily understood by the average mathematician, I suggest you consider submitting it to the American Mathematical Monthly. From the website:

Articles may be expositions of old or new results, historical or biographical essays, speculations or definitive treatments, broad developments, or explorations of a single application. Novelty and generality are far less important than clarity of exposition and broad appeal.

Notes are short, sharply focused, and possibly informal. They are often gems that provide a new proof of an old theorem, a novel presentation of a familiar theme, or a lively discussion of a single issue.

(italics mine)

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