Interview with Chen Ning YANG I : Selecting your area of research



On May 19, 2012 at the Fragrant Hill Hotel located on the outskirts of Beijing, Mr. Chen Ning YANG (Yang Zhenning) participated in a discussion with students of the Tsinghua School of Life Sciences regarding the academic life of young people. In the course of the discussion, Mr. YANG responded to many of their questions. 


One student asked the following:


“Suppose that when selecting one’s research topic, you are considering one area that particularly interests you and another that’s more practical and “hot”. It’s difficult to know which area may become a gateway of future opportunities. How should you make a balanced decision when selecting your area of research?”


The following is Mr. YANG’s response:


“There is no universal solution to this problem. On the one hand, you need to give serious thought to something that actually excites you, as it may prove to be an area that you may later decide to pursue. On the other hand, possessing a one-track mind comes with its own set of difficulties. Though there’s admittedly no hard and fast rule for choosing between the two, I’ve a bit of experience to share that may be of some relevance.


“I am of the conviction that you will inevitably come up with some ideas about those things in which you take an interest. Most of the time these ideas don’t come to fruition, but that doesn’t mean that the ideas were therefore of no use. 


“When I left for America to pursue my studies, it occurred to me on the ship that I had only studied theoretical physics in China and had yet to perform any actual experiments (it wasn’t possible in Kunming at the time). But I knew that all the sciences, including physics, were built on experimentation. So I figured I had better study experimental physics in the US, and produce a paper on it. Later on, I spent eighteen months working at a lab in the US, a period that proved to be highly unsuccessful. The reason was that I just didn’t have enough aptitude in experimentation. After I became sufficiently aware of this, I decided to pull the plug and give up my pursuit of experimental physics.



“At the same time, I had been conducting some theoretical research and found an advisor by the name of Taylor. Taylor was the first man to discover a certain trick in the process of building the hydrogen bomb. He began by giving me a research topic, on which I had produced some preliminary results. He was satisfied with the results and directed me to begin writing papers based on my results, and I soon found myself facing a dead-end, because further research would involve lots of approximate calculation, the results of which I couldn’t verify with any precision. So, after working on it for a week or two, I reported to Taylor, who appeared surprisingly unbothered; he just went ahead and assign me another project. After going through this a number of times, I came to understand his way of doing things. When it came to research, his values were starkly different from mine: he regarded something as a success even if the results were less than accurate. This certainly wasn’t my way of looking at things.


“So even though I kept in touch with him, by 1947 I began to seek out projects of my own. I worked on three or four, most of which ‘died a natural death.’ I found a good deal of related literature, but either couldn’t seem to make sense out of it or, after making sense out of it, wasn’t able to put it to good use. On top of that, my experiments were a total flop. So the year 1947 was certainly not a particularly cheery year for me. In a letter I wrote to a friend, I described that year in a single word: ‘disillusionment.’ After all, while at Kunming I had thought of myself as a ‘textbook’ student, but in America it was as though I was failing at every turn. Later, though, three of the four areas of theoretical research I mentioned previously ended up yielding fruit. Some of that fruit came three years later; for others it took over a decade.


“The projects I worked on in 1947 left me scratching my head, but that doesn’t mean my energies were wasted. As I witnessed advancements in other fields, I realize that, I could often ‘transplant’ theories from another field for certain problems I have in my own research. The point of this is, if your knowledge of a given subject did not bring about immediate success, your efforts were not necessarily spent in vain. The unsuccessful experience, once tucked away in your mind, may later bear fruit after the seed of a new discovery is sown. These, at least, are some of my personal thoughts on this matter.”

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