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