How to find interesting research problems
I strongly disagree with the "find a list of open problems" approach. Usually open problems are quite hard to make progress on, and I'm thoroughly unconvinced that good research is done by tackling some hard but uninteresting problem in a technical area.

That being said, of course solving an open problem is really good for academic credentials. But that's not what you are asking.

Research is a process designed to generate understanding at a high level. Solving technical problems is a means to that end: often the problem and its solution illuminate the structure or behavior of some scientific phenomenon (a mathematical structure, a programing language practice, etc).

So my first suggestion is: find a problem that you want to understand. Research is fundamentally about confusion. Are there some specific topics you are interested in, but that you feel you have a fundamentally incomplete comprehension of, or that seem technically clear, but that you lack any good intuition for? Those are good starting points. Follow Terry Tao's advice ask yourself dumb questions! A lot of good research comes out of these considerations. In fact, this whole page contains a lot of good advice. Note that if you are looking at a well-explored problem or field, it's unlikely you'll get original insights right away, so it's important to read up on literature concurrently with your own explorations.

Second, don't discount communicating with your Professors. Ask them about their own research, not necessarily about projects they want to give you. Engage in a conversation! This helps you find out what you are interested in, but also what the research landscape looks like in their field. Research doesn't happen in a vacuum, so you should speak to your fellow students, PhDs in your department, go to talks and workshops at your university, etc. You'll find that being immersed in a research environment helps you do research a lot more than finding a list or specific problem and locking yourself in your office.

Finally, I would suggest working on something small. Research is bottom-up much more than it is top down, and it's rare that a very simple task (writing a proof or a program) turns out to be as simple as you expected it to. Doing several small projects that are not research-scale (expanding on homework, writing up an explanation of something you learned) often build up into genuine research level stuff. It's common to try to "go big" at the beginning, but that's just now how our brains work.