I have a soft question that is interesting for me in some aspects. I appreciate your answers and comments about it.

Four years ago, one of my friends in MIT, in the biology lab, had working on neuroscience and specially he worked on Deja-Vu phenomenon. When he asked me about writing a program with Matlab for simulating this phenomenon with a network of cells that they want simulate the Sinc function, I found that there are many good theorems in graph theory that can be useful for his research. When I suggested him this idea, he found it very interesting.

My question are about this event in a little bit different way. Is it possible that we publish a paper in some mathematical journals that:

1) The only new thing in the paper is relation between a real phenomena and a field of mathematics that is well known. For example, we just model the controversy with bandwidth problem, and no more things just using the theorems that proved for bandwidth problem.

2) This paper does not have new theorems as like as theorems that are common in mathematical papers. This paper just use mathematical theorems in its direction.

Also, do we have some mathematical journals that publish such a papers? And if yes, is there some evidences for this type of publication?

Maybe someone think about the Hilbert Spaces and quantum mechanic. But, in my view, this is not the case. We use Hilbert spaces to model some aspects of quantum mechanics and we get some new results and theorems in quantum mechanic. If we want to think this relation, the paper only must be contain the modeling of quantum mechanic by Hilbert spaces and no more.

Briefly, suppose we found a connection between a real phenomenon and a field of mathematics that can be acceptable or a new view point for analysis the phenomenon. For example, if we found a relation between Darwin's evolutionary theory and a game on graph, is it possible that we can publish such a results as a paper in a mathematical journal? And what kind of mathematical journal is good for this work?

Sorry me for long question.

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    $\begingroup$ Probably a paper showing "there are many good results in graph theory that are useful in neuroscience" would probably not be publishable in a graph theory journal, but try a neuroscience journal. Or a multidisciplinary "applied math" journal. $\endgroup$ – Gerald Edgar Mar 28 '13 at 13:15

Oh yes! Establishing a connection between some class of natural phenomena and a well known field of mathematics can make you famous. And you do not have to prove new theorems. The most striking recent example is Benoit Mandelbrot. According to the Google Scholar he is THE MOST cited mathematician of all. And all his activity was exactly as you describe. Even before fractals, he was looking for new connections between "well known" fields of mathematics and real world. For example he was looking for "stable probability distributions" everywhere, "power laws" etc. But his greatest success was "fractals". The relevant mathematics was known for about 50 years. Well known to a very narrow circle of specialists, as it happens to most areas of pure mathematics. He invented a catchy word "fractal" and then showed by examples that "fractals are everywhere". I don't know a single new theorem that Mandelbrot proved. But his influence on mathematics and science was really enormous.

On a smaller scale we have "Kramers Kronig" relations (see wikipedia). Which is nothing else but the "well known" Sokhotskii-Plemelj formula. It is not important that Kramers and Kronig discovered these known relations independently. What is important is that they proposed a physical interpretation. And there are thousands of examples like this. You can even receive a Nobel prize by establishing a new relation to the real world of some well known mathematics.

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  • $\begingroup$ Dear Eremenko, your answer was interesting for me, since I did not know that Mandelbrot did not prove new theorem in fractal geometry. I think general relativity and Non-Euclidean geometry has same story. Einstein just found the relation between his theory and a suitable geometry. $\endgroup$ – Shahrooz Janbaz Mar 29 '13 at 9:26
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    $\begingroup$ You cannot compare Einstein with Mandelbrot. Einstein discovered a lot of great new things in physics. Mandelbrot did not discover new things. He brought the "known" things to the attention of "wide audience". But very successfully:-) $\endgroup$ – Alexandre Eremenko Mar 29 '13 at 12:46
  • $\begingroup$ I would say that KK relations are an application of the SP formula. By the way I didn't know that was the name of that identity (often quoted for distribution in physics). Thanks! $\endgroup$ – lcv Mar 6 at 19:38

There are a gazillion of papers like that. Actually, that's how this lowly talking duckling roles when not proving mathly-hardcore theorems.

Where to submit depends on the nature of your paper. You may have to adjust your writing style and even change the content to an extent. Either way, the golden rule I learned from my advisor and postdoc mentors is that you write your paper for your target audience and submit where they do research.

Since shiny papers by great researchers like nobel laureates may not be extremely practical examples your average guy can easily reproduce, here are how I usually do, just so you know there are a lot of mediocre examples like that too. (No. This is not a shameless self-promotion of my papers. Honest!)

A typical example of things like what you described happens when you find an equivalence between a well-studied math object in your field and something that's seemingly unrelated in another field. For example, I was reading this paper published in Science about how you can exploit Bell pairs to correct the effect of decoherence for quantum communication and another paper by the same authors published in Physical Review A about how that idea and state-of-the-art coding theory may go together. I also did a serious amount of research on this myself and actually published one paper. But after a while, I suddenly realized that what we'd been looking at is, after all, exactly the same as a fundamental class of combinatorial designs (with some caveat in fine print which I omit).

With this equivalence, I was able to import known classical results in design theory; I described what kind of quantum code their method must end up with and gave bounds on code parameters and whatnot without really proving anything except the equivalence. In this case, the target audience was coding theorists, design theorists, and physicists who read said two papers. So I chose the journal that has exactly this audience.

I could submit it to some physics journal, but such a journal wouldn't attract coding theorists and design theorists; the point of my paper was to show an example of how design theory, coding theory, and quantum error correction interact. A specialized combinatorics journal wouldn't be the best choice either because that's not where quantum physicists usually come. So I picked a journal that has a dedicated section for quantum information and is read by both mathematicians and electrical engineers. Incidentally, the editor asked us to translate some part of the original manuscript into the language of coding theory, so it's important to consider what the majority of the journal's audience is familiar with.

You can still do serious mathematics too if you like even if you just found an equivalence or new application of known math. For example, when I was a grad student, I was given a design theory problem that an engineer at nVidia brought to my mentor. I got curious about the computer engineering behind it, and I found out that the problem actually stems from a more general VLSI testing technique which Intel developed years ago. And I noticed that this general version can be understood as a problem of finding a linear hash function with certain nice combinatorial properties.

This combinatorial problem got me, so I formalized the technique Intel used to use and did purely combinatorial research. The direction of research I took and the results I got was too math-centric, so my paper wouldn't be extremely attractive to people making money in real life off of the kind of computer engineering I did some math about. But I couldn't help it because I got more interested in the math problem I defined by (obviously overly) generalizing the original engineering problem. So I wrote my paper the way (applied) discrete mathematicians would do, and submit it to a very mathematical journal that also deals with electrical engineering.

One thing you might want to note is that such papers may take longer to get published. For instance, editors may have hard time finding appropriate referees. If you're connecting two fields, the editor may need someone who speaks two previously unrelated subfields or find it difficult to convince potential referees that they can understand and judge your manuscript; your paper may look frightening at first glance to a potential referee who only knows one of the two fields well. And if your paper does require a substancial amount of knowledge in two fields to check validity and judge its quality, you don't expect your referees would return their reports in a month.

In any case, there are a lot of examples like your case. And it doesn't need to be an all-time-most-cited paper either. After all, if you're doing mathematics that you find cute and interesting, chances are someone in a different field was/is/will be thinking about a similar thing in a different scientific language. And pure math shines when you find such relations because of its rigor and generality.

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In the last paragraph, you answer your own question.

Every article must contain something new. A new in which field of science? If in biology, then it must be submitted in a biological journal (e.g., in Journal of Mathematical Biology). If you succeed to use Darwin's evolutionary theory in games on graphs (:-)) then you can publish your results in Journal of Graph Theory.

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Here's a practical example: This paper (now considered a classic in the field with 120+ citations) connected the Thurston-Neilsen surface classification theorem with the problem of mixing in fluids.

Boyland, Philip L., Hassan Aref, and Mark A. Stremler. "Topological fluid mechanics of stirring." Journal of Fluid Mechanics 403 (2000): 277-304

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Further journals devoted to papers linking mathematics with other scientific areas are the following:

Mathematical medicine and biology;

Bulletin of mathematical biology;

Computers and mathematics with applications;

Journal of mathematical imaging and vision;

Mathematical geology;

Mathematical geosciences.

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Some journals:

J Theor Biol

PLoS Computational Biology

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