How to start doing significant research? I'm a graduate student in applied math (applied probability, asymptotic etc.). I have written several articles on either solving "small" problems, or developing particular methodology/techniques towards certain type of problems. I'm at a stage where I have lots of ideas and if I want to I may be able to work out the details and write a few papers based off of them. 

But none of these things are anywhere near significant much less ground-breaking etc. My advisor said a really good PhD is supposed to make ground-breaking contribution in just one problem/direction, instead of doing petty works in three and put them together to form a "pseudo-thesis". I know what exactly what he is referring to but have no clue where to start to searching for those ground breaking ideas. 

My advisor does not like to suggest ideas/problems to me because he said he doesn't know what would be ground-breaking either or else he would do it himself than gift it to me. 

As of now, all my ideas do not seem to carry much strength in the sense that they do not withstand much investigation or turn out to be "paraphrasing" classical paradigms. I suspect that I may need to probably read beyond my field because I reckon everyone in my field pretty much is familiar with the same set of literature and has a similar way of thinking. So they have exhausted great ideas that are possible under that mindset over the decades and only leave relatively small "fruits" for me to pick up. 

My advisor said it may be good to read quantum physics as he himself is reading that and sees "lots of potential" in cross-disciplinary investigation. It would be a big investment for me because I don't know nothing about physics beyond Newton's law. But I'm in my second year so there is still time for lots of things and I think I'm tempted by the idea of learning physics and do cross-disciplinary research, although I'm keenly aware of the risk. Is learning a completely new field a good pathway towards big discovery? Should I take the risk as a PhD student? How do people stumble upon big discoveries? Is there general guiding principles behind this? 

Thank you.
What you are describing is certainly not good advising, unless you have cherry-picked some particularly negative quotes and taken them out of their context.

It is true that monolithic and groundbreaking theses are regarded higher than "stapler theses" (3-5 papers combined into a thesis), but your reputation will most likely not hinge on your thesis -- and writing several papers early is most likely better for it than writing a really good thesis. (Keep in mind: You will be applying for jobs before your thesis is out! And while those jobs will not be permanent ones, it is still very important to catch a good one, since it will influence your ability to do good research in the postdoc period. In your application, a written paper counts more than an unwritten thesis, no matter how important the latter promises to be.)

Another downside of "one big project" theses is that they are more likely to fail. If 1 of the 5 papers in your "stapler thesis" is revealed to be non-novel (and that happens in most active fields, particularly when different schools use different notation and don't communicate well with each other), your degree probably won't be delayed. If the main result of your monolith thesis turns out to be non-novel, then it may be a serious problem. And that's all assuming that you do win your bet and get that one really good result.

I have written a "stapler thesis" myself (actually the worst kind, without even a Chapter 1 that connects everything; admittedly I do a lot of exposition in my papers). I have seen many "stapler theses" from MIT students who went on to do great work. There is no stigma in them; you can do better, but someone can always do better.

As to this:


  My advisor does not like to suggest ideas/problems to me because he said he doesn't know what would be ground-breaking either or else he would do it himself than gift it to me.


The honesty is refreshing, but perhaps he should not be suggesting you to fend on your own then? Graduate students are usually not very good at recognizing which directions have promise and which are stale. This is an advisor's job. If the advisor cannot do that, he should then give the student something more concrete and incremental to do.


  My advisor said it may be good to read quantum physics as he himself is reading that and sees "lots of potential" in cross-disciplinary investigation.


This is a very dim and faraway lighthouse to steer towards. If your advisor is not offering you anything more concrete (at the very least, some reading, and not just introductory textbooks), then you can just as well ignore it for your thesis. Everyone and their dead cat knows that quantum physics is connected to probability; this is not exactly a hot scent.