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How I transformed into a senior PhD student

May 27, 2019

I previously wrote about the struggles of junior PhD students who don’t know how to do research. Here’s how I got rid of those problems and finally turned into a senior PhD student.* Importantly, I am fortunate to have a great advisor who was willing to wait for me to grow while being his student.

I was one of those less productive PhD students who did not solve any legitimate research problems in the first N years of their PhD. As a result, when some of my peers were ready to graduate, I still had no convincing evidence if I was on the right track or not. People were worried about me, and I wondered where my time has gone. People often base their self-esteem on their accomplishments. If you reach a milestone, it’s easy to convince yourself that time was spent wisely. On the contrary, if you worked for a long time without solving any problems, you may doubt if you did any valuable things at all.

Don’t think like that. Count the invisible accomplishments. Unsuccessful research experience may turn into meta-research skills. Here’s mine:

  1. At some point, I was given a cool project. I was ambitious and wanted to support the coolest benchmark first. I did not make any progress for two weeks. This experience convinced me that the smallest and dumbest benchmarks can be surprisingly valuable, since larger benchmarks often have features that distract us from the core problem.
  2. At some point, I knew little about the standard techniques in the field and could not think efficiently about any technical problem. However, whenever I started to read about a classical concept, there was always someone who kindly told me that I did not need to read about it “because it’s simply X.” If I read too much about old stuff, there’s no time for new research. A year later I finally realized that I shouldn’t have listened to this advice. These experts summarized the concept as “simply X,” but I could not come up with this summary. After I spent the necessary time in the following year to learn the fundamentals, the field suddenly became approachable. This experience convinced me that I should insist on spending time to read about things that I’m supposed to know.
  3. At some point, my advisor suggested that I could extend an existing system, Y, with a potential idea. I took this project seriously, tried to understand Y in full detail, and thought about integrating the idea into Y. Weeks later, our collaborator found out that the idea was not applicable to Y or other similar systems. This means that I did not need to understand Y to begin with. It was sufficient to understand the basic properties. This experience convinced me that the projects that my advisor suggests are just cues that inspire new ideas. Since then, I became more flexible about research goals, changing problem definitions as needed.
  4. At some point, I wanted to do research on Z with a potential idea, because everyone knows how to do Z and I wanted to do it too. So I read papers to see if the same idea had been published before. I was initially happy to find out that the specific idea was not done. However, the most closely related paper was published about ten years ago, and the bulk of the literature on Z were published in the last century. Hmm, something was not right. The most creative people had stopped doing Z long ago. It became clear that the most rewarding problems in Z had been solved and that our idea was too incremental. This experience made me appreciate fresh ideas that sound isolated to the rest of the world, as opposed to ideas that sound like something people must have already studied extensively.
  5. At some point, I needed a project. My first and only paper was being rejected for the fourth time.** From all those negative reviews, I learned how to reject almost any paper. My advisor tried to help me find a project, which I needed, but I immediately used my “wisdom” to refuse all of his brilliant ideas. I didn’t want to write a paper that was clearly going to be rejected. But I still needed a project, and couldn’t find one. Then, one day, a post-doc in our group praised one of my advisor’s ideas (which I had strongly resisted) as very interesting. He explained why. Then I remembered that all research papers are imperfect and we should appreciate their interesting insights.

After all this unsuccessful experience, I suddenly “got it.”

In the second half of my Nth year, I started to work on one of my advisor’s ideas that I initially resisted (4,5). My advisor first guided me to solve some small, dumb problems (1). As we understood the landscape better, we solved a series of larger problems (3). Then we got stuck, and we simplified the problem (3) and came up with an approach that was similar to some concepts I learned in the previous year (2). It took us another year to fully implement that project.

The grind lasted some time, didn’t look great, but was helpful.

Update on Sep 12, 2021: After years of exploration, the crazy idea (5) turned into concrete results in a series of publications. I am grateful for having an advisor who can train students to make crazy ideas come true.

 

Footnote

* More concrete PhD stories by other people, with excellent advice: List of PhD reflections by Stephen Tu and Counter-Advice for the PhD by Jean Yang.
** After five rejections, my first paper finally got accepted on the last day of my fourth year of PhD.

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