How to make your small ideas into a research paper?

Question

I am a computer science PhD student who works mostly in theory. I always have multiple ideas in my mind about the research problem I am working on and also on problems which are related to my research. Many times my ideas were vague and not important, and many of my ideas have led to algorithms which are not in themselves enough for a paper. In the last couple of years I have given many ideas to my labmates and others. My colleagues say that some of these were very good, but so far, I have not able to find anything so big that it becomes a paper. Is there any way to makes my ideas more valuable and more significant?

Question: How to make your small ideas into research paper?

Answer 1

One of my biggest regrets is not writing down small ideas. There were waiting for a better time. But usually this time never came - either because I didn't find a good way to expand on the project, or because new projects left little time.

In There are no projects like side projects (which I wrote after finishing my PhD) there is:

If you have a great project, do moonlight. Don’t wait for better times, because they won’t come. Maybe you overstate the need of money, institutional support or social confirmation?

Depending on the project, it can be a small draft (e.g. with a theorem and some comments on possible approaches to prove it) or a GitHub repository with code and some description.

Once something is shared, there are two main benefits:

• you can talk about it / send it to your colleagues,
• you made some progress, even if it is a small step, it's strictly more than nothing.

Occasionally, during the writing phase you may:

• see how to expand on it,
• or realise that actually you already did a lot,
• or discover that it is flawed (e.g. your proof is trivial or incorrect).

Additionally, if a few years later someone ask you - you will be able to recover it quickly, along with its core content (formulae, citations, etc). Sharing means that you can share it with your future self.

Is it just a one-page LaTeX note? Just write it.

Answer 2

If you have an interesting idea, but it is not yet enough for a publishable research paper, write it up anyway, in whatever form you can, and then you have a partial research paper sitting there ready for expansion whenever some new insight or aspect of the problem reveals itself. These partial papers might sit in your folders for months, or years, and some of them will come to fruition and become valuable papers, and some will just remain interesting ideas that you never developed fully. If you make the effort to write them up partially when they are just a half-developed idea, you will have a useful reference document to record your thoughts (and remind you of what you were thinking), and something to add to when you get flashes of inspiration.

Here are some suggestions for how to (eventually) turn your small ideas into research papers:

• Write up your "small idea" as if it were a full paper: This requires you to formalise your idea, put it into the language of your discipline, explain its context, etc., and situate it in the context of literature on some broader problem. Once you have written up your idea, this gives you a useful reference so that you can understand the problem and its context, and remind yourself of your idea and the progress you have already made.

• Look for applications of your "small idea" to concrete problems: Keep your idea in mind and look for concrete problems where it can be deployed to add value. If your idea requires some variation/adaptation to a new problem, think about what changes are required and whether this leads to a broader idea or methodology.

• Look for generalisations of your "small idea": Small ideas often lead to larger ideas about problems that are more general than the initial problem for in which the idea was formed. Be on the look-out for other situations where your small idea is applicable, and see if this leads you to a general class of problems where your idea is applicable.

• Bounce your idea off a colleague who finds it interesting: This can potentially start a collaboration, or give you some additional information that might tell you where to look for more material, or give you some additional lines of thinking for how to pursue your idea.

• Re-read your partially written papers periodically: When you are bored and want a change of subject, pull up your directories of old half-written papers and read a few of them to jog your memory of all your past ideas, and see if any of the pique your interest. You may find that since you last read these you have accumulated some relevant knowledge that adds to the idea, and this can spur some further work that adds to your idea.

• Let your sub-conscious take over: Once you have written up your idea to whatever partially-completed state you can get it to, and you have thought yourself to a dead-end, stop thinking about it and let your subconscious take over. Allow yourself to work on other problems, but come back to it periodically to see if there is anything more you can add.

Your problem reminded me of a passage from the physicist Richard Feynman, where he talks about the importance of "playing" with your subject matter, even if this has no obvious importance. Here is Feynman (1985) describing how an interest in a silly little toy problem led to him receiving the Nobel prize in physics:

Then I had another thought: Physics disgusts me a little bit now, but I used to enjoy doing physics. Why did I enjoy it? I used to play with it. I used to do whatever I felt like doing - it didn't have to do with whether it was important for the development of nuclear physics, but whether it was interesting and amusing for me to play with. When I was in high school, I'd see water running out of a faucet growing narrower, and wonder if I could figure out what determines that curve. I found it was rather easy to do. I didn't have to do it; it wasn't important for the future of science; somebody else had already done it. That didn't make any difference. I'd invent things and play with things for my own entertainment.

So I got this new attitude. Now that I am burned out and I'll never accomplish anything, I've got this nice position at the university teaching classes which I rather enjoy, and just like I read the Arabian Nights for pleasure, I'm going to play with physics, whenever I want to, without worrying about any importance whatsoever.

Within a week I was in the cafeteria and some guy, fooling around, throws a plate in the air. As the plate went up in the air I saw it wobble, and I noticed the red medallion of Cornell on the plate going around. It was pretty obvious to me that the medallion went around faster than the wobbling. I had nothing to do, so I start to figure out the motion of the rotating plate. I discover that when the angle is very slight, the medallion rotates twice as fast as the wobble rate --- two to one. It came out of a complicated equation! Then I thought, "Is there some way I can see in a more fundamental way, by looking at the forces or the dynamics, why it's two to one?"

I don't remember how I did it, but I ultimately worked out what the motion of the mass particles is, and how all the accelerations balance to make it come out two to one. I still remember going to Hans Bethe and saying, "Hey, Hans! I noticed something interesting. Here the plate goes around so, and the reason it's two to one is ..." and I showed him the accelerations. He says, "Feynman, that's pretty interesting, but what's the importance of it? Why are you doing it?" "Hah!" I say. "There's no importance whatsoever. I'm just doing it for the fun of it." His reaction didn't discourage me; I had made up my mind I was going to enjoy physics and do whatever I liked.

I went on to work out equations of wobbles. Then I thought about how electron orbits start to move in relativity. Then there's the Dirac Equation in electrodynamics. And then quantum electrodynamics. And before I knew it (it was a very short time) I was "playing" - working, really - with the same old problem that I loved so much, that I had stopped working on when I went to Los Alamos: my thesis-type problems; all those old-fashioned, wonderful things.

It was effortless. It was easy to play with these things. It was like uncorking a bottle: Everything flowed out effortlessly. I almost tried to resist it! There was no importance to what I was doing, but ultimately there was. The diagrams and the whole business that I got the Nobel Prize for came from that piddling around with the wobbling plate.

Answer 3

While I agree with Piotr Migdal's advice about writing down your discoveries, even small ones, I don't think it directly answers the OP's question.

In my opinion, you should be clear on two things:

• First, generally you will have more ideas/questions than you have time to seriously work on.

• Second, while (rough) ideas are easy to come by, well-thought out plans for doing something serious and novel generally take a lot of work.

So when you have an idea you like, sit down and take the time to think about it thoroughly. See how far you can push it. Sometimes it will lead to a nice nontrivial result you can publish (directly or indirectly) but often it won't go anywhere. Or maybe it will go somewhere when you come back to it years down the road. That's the nature of research.

Also, sometimes when you have a little result, sometimes it's hard to decide whether you should try to publish it. It really depends on the situation. But try telling some people about it, and maybe they'll provide feedback or suggest possibilities to do something further with it.

Answer 4

I am not very knowledgeable about the sciences, but I am an M.A. Student who has done several research-projects (nothing worth writing home about).However, as someone majoring in TESOL, and as someone working on my Teaching of Composition Certificate, I have studied a fair amount of theory. Combining my theory with my experience, I would suggest that you formulate your research questions, even if they don't seem significant, and begin writing your paper. Initially, just worry about getting your ideas down, and do not worry about grammar, style, or formatting. Many studies of writing indicate, as does my own experience, that as you write you will stimulate thought and new knowledge will emerge. The writing process, itself, should help you formulate more and better ideas as long as you are willing to abandon some of your initial ideas, assuming they no longer apply as you progress. The very act of writing the paper will often help clarify and expand your thinking in a way which hopefully will inspire you to find some really exciting research questions. If necessary, walk away from it for a day or more and come back to it for a fresh perspective. Once you find the question or questions that you are interested in, like the old adage--A problem well defined is a problem half solved. I hope this is helpful, and I wish you the best of luck on your project!