Math papers where the only issue is that someone else could've done it but didn't Do editors for top math journals ever read a submitted paper, agree that there are no mistakes and the result is new, yet still reject it on the basis that this is a top math journal and someone could've done that before but chose not to? Maybe some arrogant mathematician goes "I could've proven that in a day or week but didn't because there's better stuff to do."
I'm wondering because this seems to potentially fall into the category of results that are correct but not important enough. It appears the importance of a theorem depends not just on how many people care about it, how much it connects to other results, and how it can be applied, but also as a byproduct how many people have tried to prove it and failed. This last point is where the previous paragraph is relevant.
Note that I'm only counting attempts by mathematicians (let's say at least a degree in math or peer reviewed research for starters) since some of the most famous conjectures receive tons of crackpot attempts after becoming famous, in which case cause and effect are reversed. In fact, most problems in the scope of this question would be slightly famous at best.
If only a few people (or perhaps just 1) have tried and failed, does that discount whoever eventually succeeds? There are way more questions than there are people and hours around to answer them, so perhaps lots of people would like an answer (in the sense that we would like an answer to many questions but cannot attempt every question we're interested in) but only a few people are putting in the time. In the case where few people try because they believe it's too difficult, the paper probably will be accepted. However, if people think it's within their reach and don't try for other reasons, we may end up with a situation similar (but more respectful) than the one in the 1st paragraph.
 A: As Sam Hopkins comments, the short answer to the stated question is "yes, all the time." You'd be hard-pressed to find a professional mathematician who hasn't received a referee report that basically boils down your first paragraph. Often, the referee or editor can't find anything mathematically wrong with the result, but they reject the paper on the basis that it's not at the right level for the journal, meaning the result or techniques used are not interesting or novel enough, in their view. Essentially, this means they think the work could have been done by many people but wasn't really worth the effort.
The rest of the OP seems to be asking about whether or not it matters if someone else has tried and failed. In fact, it does matter, and it makes the paper more likely to be published if someone else has tried and failed, rather than less likely as the OP suggests.
Let me give you a concrete example. In 2017, my coauthor Donald Yau and I wrote the paper Arrow Categories of Monoidal Model Categories. This paper was published in 2019 in Math Scandinavica. In it, we proved a fact that I would not normally have thought would be worthy of a paper in its own right. However, because the statement had been left as an Open Question by a well-known mathematician in the field (Mark Hovey), we were able to frame the paper as "answering a question of Mark Hovey" and I think that probably helped it get published.
For an example in the other direction, my co-author Michael Batanin and I wrote a paper, Left Bousfield localization without left properness, that I think is definitely worthy of a publication. It shows how to side-step a problem that has bedeviled mathematicians in the field for a long time, and has zillions of examples illustrating the power of the approach. However, because it was left as a remark (4.13) in a paper by Clark Barwick, it has been much harder to get this paper published. I got a rejection that essentially boiled down to "Clark Barwick knew how to prove this and didn't think it was worth writing down."
It is worth noting that the paper in question was one of Clark's earliest, and he later wrote a great essay about The Future of Homotopy Theory where he lamented this kind of thing. He wrote:

We do not have a good culture of problems and conjectures. The people at the top of our field do not, as a rule, issue problems or programs of conjectures that shape our subject for years to come. In fact, in many cases, they simply announce results with only an outline of proof – and never generate a complete proof. Then, when others work to develop proofs, they are not said to have solved a problem of So-and-So; rather, they have completed the write-up of So-and-So’s proof or given a new proof of So-and-So’s theorem. The ossification of a caste system – in which one group has the general ideas and vision while another toils to realize that vision(6) – is no way for the subject to flourish. Other subjects have high-status visionaries who are no sketchier in details than those in homotopy theory, but whose unproved insights are nevertheless known a
conjectures, problems, and programs.

He even includes a side-note saying

(6) only to have their paper rejected with lines like the following, from a colleague: "After So-and-So’s [sketchy] work, it was essentially obvious that such a result would be possible, given the right framework."

So, based on that, I have to conclude that if he had a time machine, Clark probably would have written his Remark 4.13 as a Conjecture and then I could have published my paper saying I "proved a conjecture of Clark Barwick." I confess that I'm guilty of very much the same kind of behavior. I put a paper on arxiv in 2014 announcing a result that wasn't on arxiv till 2017 and one researcher told me my remark discouraged him from working on the project. I regret that. Nowadays I try to put many more Questions, Conjectures, and Problems in my papers, e.g., this one that just got accepted for publication.
So, to conclude, I call upon anyone who has read this far to include named/numbered Conjectures, Questions, and Problems, and at all costs avoid Remarks where you claim things are true but don't write out the proof. Let's make the field friendlier to young people and help them get their work published, while at the same time incentivizing them to build on our work by answering questions we explicitly leave. I wrote something before to this effect here.
A: The short answer is yes.  As far as I know, the typical questions that a reviewer asks are (in this order):

*

*Is it correct?  - Your example passes this check because it all seems to be correct and there are no obvious flaws in the proofs.

*Is it new? - Strictly speaking, yes, as no-one has formally written it all down before, so your example passes.

*Is it interesting? - Now crucially, your example fails.  Yes, it is new in a sense and it looks to be correct, but it is not saying anything which is really interesting.  It could have been done pretty easily before with existing techniques, but just no-one had the time to do it or they couldn't be bothered etc.

Criterion 3.) is admittedly quite subjective, but it is nevertheless considered to be a crucial criterion when deciding if something merits publication in a certain journal.
One could also add a lesser but still important criterion:


*Is it a good fit for that journal?
A: (A bit less than a complete answer; too long to be a comment. Slightly opinionated.)
Yes, top journals do this. That said, publishing in other journals is ok. And sometimes an idea seems obvious to one person only seems obvious because they are now reading someone discussing it or proving it. And even when yes it would be obvious to some people, that's still ok.
It is genuinely helpful to have in the literature papers that might be easy or obvious to some people. One shouldn't think that because something isn't going to be published in a top journal that there's anything wrong with it. That doesn't make it not good mathematics.
In that context there are two types of papers which are much helpful enough to be worth stating explicitly as in the yes-that's-good-math-which shouldn't-be-published-in-top-journals-and-that's-ok category. The first is papers which are primarily computational where there's at most only minor improvements in algorithms used, but where one is taking advantage of better computing power. That said, when one does publish those sort of papers, an additional goal should be to make them have at least better expository results. The second is papers which take a bound using some asymptotic estimate like the prime number theorem and then either make that bound explicit or use improved versions of known bounds. For example, there are a lot of papers which use Rosser and Schoenfeld's explicit bounds on the PNT to get explicit bounds on some other object of interest. Since we now have a whole bunch of bounds which are tighter than Rosser and Schoenfeld, using them to tighten up the results which depended on Rosser and Schoenfeld can be helpful. But it is obviously not the sort of thing which should go in a top tier journal.
I'd really be happy with both of these sorts of papers getting their own explicit journal. Something like "The Journal of Straightforward Improvements."
A: Let me take the liberty of rephrasing the question slightly. Does the mathematical community put undue emphasis on accomplishing something "difficult," and thereby undervalue certain highly original theorems and conjectures?  I think that the answer is yes.
I have frequently encountered mathematicians who make snap decisions that some fact "looks easy to prove." Sometimes, that judgment is way off, but it's hard to talk them out of it except by presenting evidence that a lot of people tried to prove it and failed (and even then, they may just conclude that all those people were just idiots).  This means that if you come up with a highly original theorem or conjecture for which there is little or no prior evidence that it is hard, you may have a difficult time getting it published or otherwise granted respect.
To be fair, it's true that if not a lot of people have tried to prove something, then indeed there's not much evidence that it's hard, and it may be evidence that the statement in question is not that interesting (otherwise, why wouldn't someone else have already been led to consider it?).  However, I find it somewhat ironic that the more original an idea is and the simpler the proof, the less respect it tends to get.  In official statements, we claim to value originality and simplicity of proofs, and we disavow the view that mathematics is a contest to see who is the "smartest," but our actual behavior belies our words.
To mitigate this tendency, I try to encourage people to be suspicious of their own instincts that something is easy.  By the way, we see this sort of thing here on MO quite frequently, where someone instantly votes to close a question as being too trivial, without having the slightest idea how to answer the question (which often turns out to be rather interesting and difficult).
