I have found a new solution for a problem in Computational Geometry but after intensive research learned that the key idea was already known in a different field of mathematics but also hard to find in the literature of that field.
Question: What are criteria that allow one to decide whether or not to publish results that are based on the rediscovery of a result that is known but not in field that the intended publication is targeted at?
Since you asked if this can be publishable, and did not specify beyond that, I will discuss the possibility of publishing an expository article. You have a new technique for people in Computational Geometry. If people in your field have a hard time reading in the other field, you will do a great service by translating this into familiar notation and terminology. This may not count in some scheme your dean uses to gauge productivity, but it might gather a multitude of citations.
Of course it might be publishable as a research paper, or part of a research paper. If you are not about to apply for tenure, you have the option of sitting on this for a while. See what problems you can solve with this that cannot be solved by the current techniques in your field. Solve something not yet solved. Then you have a section on the technique that is new to your field and can showcase the solved problem to get that "look at me mama" section in your paper. If the new technique only makes a few existing problems a bit easier, then this is maybe not a eureka moment.
A "pure" rediscovery of known ideas (meaning, when literally the exact thing you discovered was already known) is not publishable, because it is not new knowledge.
HOWEVER. It is not uncommon for rediscoveries to be not "pure", where the researcher comes at a problem from a somewhat different point of view from the people who came before, and discovers some combination of "known" and "new" things. For example:
You found a new proof of a known theorem. That could certainly be publishable (depending on how interesting the theorem is, and how interesting and different from the original proof the new proof is).
You found a new application of a known theorem. (Bonus points: you found a new application in a different field from the field the theorem was considered important/well-known in.)
You found a new insight or point of view relating to known theorems; e.g., you noticed that known Theorem A is a special case of known Theorem B, where that wasn't known before, or some other previously unnoticed relationship between known results.
Etc.
It seems impractical to categorize all the possible ways in which a rediscovery can be argued to have sufficiently novel elements to make it publishable. The point is, there has to be something about what you did that you can try to "market" as novel. And your novelty argument has to actually be convincing to at least some people. In my opinion, "hard to find in the literature of that field" is not a convincing argument. (If you are bothered by something being hard to find, post it on your web page. Or translate it from French to English and post the translation on your web page, as I once did with a "hard to find" paper.) The argument "this was known, but in a different field of mathematics" is also a bit iffy IMO (although I can see contexts where it might offer a bit of support to your overall publishability argument). But even setting aside these particular arguments, it's possible that you can find some other way to argue successfully that what you did has some novel elements and should be published.
The usual criteria for publication in math is novelty (something new) and significance (something worth knowing). But there are two aspects, since proofs, themselves, not just theorem statements, carry information and can guide future progress.
So, while it remains a judgement call by reviewers and editors, a known theorem might be worth publishing if the proof is new and results in some insights that help push the art forward. Proofs can be more valuable than the theorems themselves, in this way. Proofs are, perhaps, a methodology, and are especially valuable when the ideas in them can be applied elsewhere.
One way to think of theorems and proofs is that the theorems are the milestones but the proofs represent the progress made to get to that point. And there may be many "interesting" paths to reach a given milestone with things to learn along each path.
So, yes, but it is a judgement call as in most things offered for publication.
If you have a new application, it's still a perfectly good addition to the literature, especially if you've done significant work to demonstrate why it's applicable.
Our company (in conjunction with the UK National Physical Laboratory) recently did some work to apply Chebyshev polynomials to correcting positioning errors in 2D and 3D positioning systems. There was nothing new in the use of Chebyshev polynomials for a mathematician, but the engineering community were not familiar with them as a more numerically stable method of applying a nonlinear mapping. We also needed to demonstrate that this correction method was indeed supported by the data, and even more interestingly, that we could reduce the data required to a practical level for manufacturing.
All of that warranted publication of a paper with our results, even though the maths of it was nothing at all new.
