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I am looking for examples of recently (last 20 years, say) published math papers such that:

  • the results/examples were fairly trivial (by this I mean anyone with the definitions and standard background in the area of research could have thought of them, but never took the time to do it, or it simply never occurred to them); and yet
  • the questions posed in the papers, which were motivated by the results, lead to future research and solutions which were non-trivial.

These should not be foundational papers in the sense that they introduced an entirely new field. Assume those papers published long ago, with books written on the subjects, etc.

I guess this question stems from a fear that my papers fit this mold. The questions (often my own) I am unable to answer seem far more intriguing than what's actually in my papers...

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    $\begingroup$ "The questions (often my own) I am unable to answer seem far more intriguing than what's actually in my papers...." I think a lot of us share that feeling. $\endgroup$ – Gerry Myerson May 19 '18 at 0:12
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    $\begingroup$ Re: "a fear that my papers fit this mold": I don't think that's something to fear, and this could even be a reason to be proud. Asking the right questions seems just as valuable in my eyes as providing the right answer. (But maybe I say so because my MO reputation comes more from questions than from answers. 😉) $\endgroup$ – Gro-Tsen May 19 '18 at 5:17
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    $\begingroup$ Seems like any paper that introduces an interesting and difficult new conjecture could be an answer to this question. I will say that unless the conjecture is obviously of great importance then editors and referees tend to be biased against such papers. If the conjecture is new then how interesting can it really be? And if you couldn't prove it then clearly you're not a very good mathematician. $\endgroup$ – Timothy Chow May 19 '18 at 13:56
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    $\begingroup$ I'm clearly against big-list lists of recent papers (with some vague requirement), since it leads to promotion of recent work, including auto-promotion. Including papers of, say, at least 40 years old would, at the opposite, be a reasonable safeguard. (Even this being said, this remains very subjective.) $\endgroup$ – YCor May 19 '18 at 19:16
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    $\begingroup$ The Andrews-Curtis conjecture. $\endgroup$ – Jim Conant May 19 '18 at 21:12
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I have a paper which may qualify, except that it was published approximately 30 years ago. It contains:

a) a simple definition, which was very natural to make in this area, b) a theorem which any specialist in the area could prove (the level of difficulty of an average MO question), and c) a conjecture.

The paper is published in a conference proceedings. http://www.math.purdue.edu/~eremenko/dvi/banach.pdf

This had a substantial effect over the years. To have an impression of this effect type these keywords on Google: "escaping set", "Eremenko conjecture". The conjecture is still unproved but there are many deep and interesting results related to it. Here is a very beautiful exposition: https://www.impan.pl/~perspectives/Rempe-Gillen.pdf

Remark. There are at least two people who proved the result themselves but did not care to publish it (this was after my paper but they did not know about it.)

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    $\begingroup$ Perhaps the goal is to be modest, but I'm not sure of the point of mentioning the paper only by MR number. To save others the agony of Googling/MSNing, the paper is Erëmenko - On the iteration of entire functions (MSN); and the queries are "escaping set" and "Eremenko conjecture" (Google prefers the latter to "Eremenko's conjecture"). $\endgroup$ – LSpice May 19 '18 at 22:18
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    $\begingroup$ @LSpice: You are right. I changed the reference. Not everyone has access to the Mathscinet. $\endgroup$ – Alexandre Eremenko May 20 '18 at 5:14
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The importance of Subhash Khot's paper on the Unique Games Conjecture derives primarily from the significance of the conjecture that he introduced, which has stimulated an enormous amount of research in complexity theory. It might not quite fit your criterion because the results in the paper are not trivial, but certainly the conjecture itself is now regarded as the main contribution.

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    $\begingroup$ Came here to post exactly this paper. I think I recall Subhash telling me he thought the only real 'content' in the paper was the semidefinite programming algorithm he put in the appendix, but even that would soon become pretty standard. But the conjecture itself was hugely influential; see, e.g., simonsfoundation.org/2011/10/06/… $\endgroup$ – Ryan O'Donnell May 20 '18 at 1:58
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The Nash equilibrium comes to mind. The proof was by a fixed point argument. The effect was immense. But the paper is more then 20 years ago.

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    $\begingroup$ Though to be pedantic, it's not the "questions" posed in that paper that led to dramatic impact later; the implications of the results themselves turned out to have great impact of course. $\endgroup$ – Suvrit May 19 '18 at 10:21
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Ralph Greenberg phublished in 1977 his thesis, written under the direction of Kenkichi Iwasawa, in an American Journal of Math paper entitled Iwasawa invariants of totally real fields. Back then, the so-called Main Conjecture was still open and Greenberg studied the vanishing of a certain invariant $\lambda_p$ partly for its own sake and partly because in certain cases it would imply the Main Conjecture. Little by little, people start to refer at Greenberg's condition $\lambda_p=0$ for totally real base fields as "Greenberg's conjecture" although he had not conjectured anything and simply studied the question.

The Main Conjecture was proven by Mazur--Wiles (1984), then reproven in greater generality by Wiles (1990), eventually proven a third time by Kolyvagin--Rubin (1992 or so) with much easier techniques. But Greenberg's question whether $\lambda_p=0$ is still alive and active, people are trying to prove it in general and the few results contained in the original thesis, albeit somehow interesting, got more or less forgotten.

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It's older than 20 years but otherwise the paper where Kashiwara and Vergne introduced their conjecture definitely qualify https://link.springer.com/article/10.1007/BF01579213

There is an important theorem of Duflo stating that the PBW isomorphism for a finite dimensional Lie algebra (in characteristic 0) can be twisted so that its restriction to the invariant part actually become an algebra isomorphism $U(\mathfrak g)^{\mathfrak g}\cong S(\mathfrak g)^{\mathfrak g}$.

The original proof is complicated and require a lot of case by case study. Kashiwara and Vergne suggest a very natural uniform proof of that result. Roughly speaking they postulate that the pull-back of the product on $U(\mathfrak g)$ to $S(\mathfrak g)$ through this twisted version of the PBW isomorphism can be written as $m\circ F$ where $m$ is the multiplication of $S(\mathfrak g)$ and $F$ is an automorphism of a very special form. Then they "rescale" it by introducting a parameter $t$, and observe that Duflo's theorem would follow from the existence of such an $F$ satisfying a certain differential equation w.r.t the parameter $t$. They also observe this would in fact imply a stronger statement, giving an isomorphism between invariant distribution on $\mathfrak g$ and its group $G$ with small suport. Their conjecture is thus really important in harmonic analysis and representation theory.

The main result of their paper is a proof of that conjecture in the solvable case, which can be done in a fairly elementary way. After that, several special cases were proven, but a general proof was given only in 2005 (by Alekseev--Meinrenken) and uses some high level machinery related to Kontsevich's proof of his deformation quantization theorem. Since then this now theorem has been connected to a surprisingly wide range of topics, including Grothenideck-Teichmueller theory, Etingof--Kazhdan theorem, quantum topology and the study of the Atiyah--Bott--Goldman Poisson structure on moduli spaces of flat connections.

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The $n!$ conjecture is perhaps another near-miss. It was posed 25 years ago by Garsia and Haiman, and the ideas in the paper are interesting and non-trivial, but the conjecture itself was probably the most interesting part of the paper, and was a major stimulus for the next ten years until Haiman finally proved it.

Along similar lines, the shuffle conjecture was introduced in 2005 and recently proved by Carlsson and Mellit. The conjecture itself was the most interesting part of the original paper and it stimulated a lot of research.

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In 1980 Charles Leedham-Green and Mike Newman published the paper: "Space groups and groups of prime-power order I". The main goal of the paper was to introduce five conjectures, namely Conjectures A-E, in descending strength. The rest of the paper was fairly technical results (as far as I understand). These five conjectures are the coclass conjectures.

The conjectures attracted a lot of attention and many people were involved in proving them. I do not recall the whole history, but Conjecture E was proved by Leedham-Green, McKay and Plesken. Then results of Donkin and Leedham-Green proved Conjecture C for $p>3$ and later on Conjecture A also for $p>3$. Afterwards, Shalev and Zelmanov proved all the conjectures for all $p$'s. Finally Shalev gave an effective proof of the conjectures.

These days there is still research done on the structure of groups of finite coclass.

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