Methodology of defining a research topic My adviser asked me to come up with a research topic for a PhD student. As I'm expected to graduate in early 2016, my mentor considered this a good "exercise" for a tenure track career. Of course, this is not intended to be final, I am supposed to propose to my adviser this topic and then it will be decided whether it is good enough to suggest a direction of a student's research. 

Based on the field of interest, I intend to propose a problem which I find interesting (and would gladly research myself, if the time permitted). To that purpose, I defined a number of milestones, covering some likely scenarios in the research progress. I also prepared around 20 papers, some of which serve as an introduction to the problems of the field of interest, while others are state-of-the-art approaches closely related to the topic.

This is basically more than I had when I begun my research. So, in that regard, I'm confident that I did a reasonable job so far. Of course, if you have any remarks, don't hesitate to add them.

My problem is that it would currently be very hard for me to come up with more than 2-3 topics prepared in that way. 

Also, I can't help but wonder whether the topic I would suggest is "good enough" to lead the student to conduct quality research and eventually to a PhD. In this particular case, my mentor will shape the topic and guide the student so there is no worry. Besides that, I am confident that the suggested topic is a problem in the field, as I thought and investigated it a long before the request came from my adviser.

I find it a bit hard to believe that I'll always have such problems ready in my head, so I assume that I'll have to start from somewhere in forming one.

So, what methodology should I follow when defining research topics?
I think this is a great exercise.  One of the hardest things to cope with in the transition from graduate student to PI is broadening your focus as you move from a "worker" role toward a "manager" role in research.  This doesn't mean you're not going to be continuing to research, but you'll likely have a lot less time to do it than you think, and you need to prepare for how you will supervise where previously you would execute.

That said, I think you're currently approaching this too much like you are going to be the one doing the research, rather than their supervisor.  I would suggest limiting yourself to finding a topic, milestones, and rough criteria for success: the rest is what you want to coach a student as they look into the background, compare in depth with alternate approaches, etc.

The other thing I would advise is that you need to separate your research goals from the goals you want the student to work on.  Every student is a gamble: some work out well, while others drop out, burn out, should never have been in the program to begin with, or just plain aren't a good match for you or your research area.  For this reason, I believe you should never have a student be critical path on an aspect of your research that deeply matters to you: that will put you in a position where you are likely to be trying to push them and micromanage them, because you are worried about the success of the work, rather than the success of the student.

Instead, think about the "paths not taken" on your research, the things that you think would be interesting and scientifically valuable, but that you aren't going to do, the sort of stuff that pads out many papers' "discussion" and "future work" sections.  These sorts of "sibling projects" to your critical path are likely to be a rich vein of seeds for student projects.