What are the benefits for a PhD student working on small problems vs solving a big problem?
[I'm an American theoretical computer scientist; some of this advice will not translate well to other fields and countries.]


  I am confused about this: should I work on one particular problem for a year and get a result (there is a high risk with this thing) or should I work on 2-3 small problems and combine them to make a result?


Neither.  You should work on problems if and only if


You find them interesting.
You enjoy being frustrated by them.
You have time and energy to work on them.
You (and your advisor) believe you can make progress on them.
You (and your advisor) believe you can convince your target community to care about them.


As a beginning PhD student, your first goal should be to publish something.  Don't worry about whether it's big or small.  It doesn't have to be important.  It doesn't have to have anything to do with your later thesis research.  It doesn't have to be in a top venue, although it does have to be in a venue that people actually care about.  Your only goal here is to successfully walk through the process of writing, submitting, revising, publishing, and presenting a research result, so that later, when your much harder research isn't going well—and that will happen—you have direct evidence that you can do publishable research.

Once you have that, your next two goals are (1) publish something at a top conference in your field, and (2) have something rejected from a top conference in your field, and then later publish it anyway.  Note that these two goals can be met by the same paper.  Satisfying these goals requires understanding the expectations/standards/style/taste of the community you're aiming for; this understanding is far more important than (but related to) whether the result is "big" or "small".  Again, both of these goals are important bulwarks against Impostor Syndrome.

If you've gotten this far, whether your realize it or not, you've built up some significant expertise and intuition that is unique to yourself.  Exploit it.  Your next goal is to exploit that and publish two or three papers on some common theme — similar tools, or similar problems, or at least similar venues.  You don't have to fix the theme in advance; you may not even understand what the theme is until you're done, and that's fine.  Your earlier papers can be used as part of this body of work, but they don't have to be.

In parallel, you absolutely must publish something without your advisor.  That can be part of your coherent body of work, but it doesn't have to be.  It can be a solo paper or with other collaborators; that doesn't matter so much.  But it is absolutely vital that your advisor is not a coauthor.  In particular, your advisor must not contribute enough to the paper to deserve to be a coauthor—gift non-authorship is just as unethical as gift authorship.

On the other hand, your advisor must be fully aware and supportive of your independent work, while they keep their hands off.  If your advisor is likely to object to you working independently, you need a new advisor.  (If your advisor's objections are dictated by your university, you need a new university.)

Once you have a coherent body of work, all that's left to do unify the presentation (especially the terminology and notation), write a coherent introduction/literature survey/conclusion, cram everything into the horrible thesis style dictated by your university, and convince your thesis committee that you're done.  Congratulations, it's a thesis!  This is the easiest of all the steps listed so far, and by far the least important.

Over time, as you gain experience and confidence, your results will naturally get "bigger" (at least on average).  Don't worry about making it happen; as long as you keep working on things that you enjoy being frustrated by, it'll happen on its own.