How to start doing significant research?

Question

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.

Answer 1

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.

Answer 2

First, a general statement: personally, I think that it is much easier to think about grand things if you are enjoying your work, can immerse yourself in it, and do not have to think about meta problems, such as panicking about needing a result in order to get a degree.

One immediate corollary that I take from this is that I like to start my students on something that is very very likely to yield a solid (not ground breaking) result in a reasonable time span, and will get them within epsilon of being able to write a thesis (I am in the UK, where students generally have less time for their PhD than in the US), while getting them to learn techniques and problems in an area where ground breaking stuff might be possible. But as others have said, the ground breaking stuff takes time and should not be expected to come before you submit your thesis. Solid work will be enough to land you a postdoc position. In light of this and of the first paragraph, it seems like a very bad idea to me to start trying to do something ground breaking when, if it fails, you will not have the material for a thesis, and I would recommend doing it in the reverse order.

Even when you become an established researcher, you are unlikely to be able to afford to sit there for 5 years working on a breakthrough without producing visible outputs in the meantime. It is therefore important to learn to maintain a steady output of good work while you are working on grander things. Since it is completely unpredictable how long the grander things will take or whether they will materialise at all, you should decouple that part from your immediate goal: getting a PhD, which is what the steady output of good work will grant you.

One last thing that you cannot do much about, but that might put things a bit into perspective: being hands-off as a supervisor is not at all the same as outright saying that they will not share their good ideas with you. I have seen some fairly hands-on and some completely hands-off supervisors, but almost all good supervisors I have seen (in pure maths) are prepared to generously share their best ideas with their students; and if they are not, then they just don't take a student.

Answer 3

My candid advice:

1. Keep "stamp-collecting"; do the "snowball" (packing snow together) thesis when you decide to leave. Don't let your advisor tell you what to do. It's VERY easy for tenured profs to say things like he did, but he has completely different risk/reward. Burning out some non-superstar advisees is like a who cares to these guys. But you care if you're the butterfly dying.

2. Keep your eyes open. Some time insights come when you are "grinding the pigments". Keep a notebook (or file folder full of cocktail napkins) with your ideas. Don't worry about differentiating small from big. Just collect them. If anything at least it gives you a parking lot piece of mind. And sometimes something comes of it after the napkins sit in the folder a little bit. Leave yourself freedom to "brainstorm" (open the goofy part of the brain, versus the editor part) at least as it comes to the idea list.

3. Spend some certain amount of time (~1/week, 20%) doing "bootleg" stuff. Just something totally different that might not work, etc. [Somehow find a way to write up all the bootleg fiddling around, even as another stamp. But that is way down the road. While messing around, put no pressure on yourself and play.

4. Don't dive down the physics rathole. That's your advisor's idea. It doesn't sing to you. Get something of your own. Plus, it's kinda not news that physics has math applications and the physickers all think they are better at it already. (Not true, but you know how they can be.)

5. Instead do something in petroleum geology, oil well completion, or even oil well economics. It's a huge area. With both existing status (not lock blockchain) AND dislocations/changes creating opportunities. Target rich and odds in your favor (like being the only guy in a power yoga class). Not like everyone trying to be the next Google or Amazon idea guy. Very hard physical problems (e.g. three phase flow). And they have lots of money--yes, even when they say they don't, they do. Plus it's of high interest to both supermajors and Halliburton/Schlumberger (best to collaborate with). And strategically of interest to the PRC. [Just building some option value.]

Answer 4

Have you ever taken a risk (scientifically)? Tried something not in books? Invented a method (even if it later turned out to not be novel)? Built a crazy device? Played around with chemicals? Tinkered with your computer outside of the usual routes - trying to get something under the hood to work?

If yes, and some of it was successful (nobody ever succeeds in everything), go ahead and start something risky, such as what you describe as overlap of Quantum and probability. Else, you have not much experience with risk, so you probably should take it a bit more carefully. You have to learn whether you can trust your scientific instinct or not.

One more suggestion: go to meetups or conferences. This is one of the best places to get fresh ideas from.