Q1: Can you share the story behind your discovery of Kosterlitz-Thouless (KT) transition? Is there any preceding research that relates to or inspires you to discover KT transition?

A1: When I accepted the postdoc position in Birmingham, I intended to shift from high-energy physics to a different field, perhaps condensed matter physics. I spoke with several faculty members to get their advice. One day, David Thouless showed me some experimental results on thin helium films, which clearly indicated a phase transition that didn’t align with existing theories. Although I was not David’s student or postdoc, and he probably didn’t even expect me to come up with anything given his very vague ideas, I decided to make efforts. After several months, I eventually came back and showed him what I got. We decided to write and publish this, and the rest is the history you’ve all known.

Q2: KT transition has challenged the conventional wisdom at the time, did you encounter any skepticism?

A2: Thouless and I were exactly the right people to look at this problem. The situation was clearly awkward because there was a conflict between theory and experiment, and the theory looked extremely reasonable. At that time, I was completely ignorant of condensed matter physics. But luckily in this case, ignorance turned out to be an advantage as I wasn’t burdened by the conventional notions, so I was free to explore new ideas with nothing to influence my thinking. We managed to solve this problem because we realized that instead of thinking about the low energy excitation, the only possibility was to think higher energy excitation, essential for the vortex excitations, the only excitations that we can destroy superfluidity.

Q3: What were the key inspirations that led you to explore topology in condensed matter physics?

A3: I have to admit, I didn’t even know what topology was at the time. I only had a vague idea that it was a branch of mathematics concerned with characterizing various shapes, but I had no idea of its importance until I had done a lot of calculations. I then talked to Thouless and he said these vortices were topological excitations, and that’s how ‘topological physics’ came into the picture. But it doesn’t change anything, because what I really did and understood was physics. So to me it was simple and intuitive. Thouless found those vortex behaviors look like topology to him. And we can bring those fancy mathematical names to physics, but underneath is physics only.

Q4: Following your theoretical breakthrough, many of the experimental verification were conducted in the years after, did those verification timelines match your expectations?

A4: After we finished and published the work, we were eager about experimental verifications. At that time, a few experimental groups were studying helium films, particularly, John Reppy's group at Cornell had been working on thin superfluid films for quite some time. So I went to Cornell for a one-year postdoc, and one day I was giving a seminar about what Thouless and I had achieved, but it seemed that almost no one really followed our reasoning. I remember that even Kenneth G. Wilson—who later won Nobel Prize in Physics 1982 – was also there and asked me a question about irrelevant variables. I had no idea what he was talking about, so I sort of hummed and hawed basically giving a non-answer to his question. But there was one single person in that room who really got it: a bright young graduate student named David R. Nelson (now professor at Harvard). From then on, we got along very well.

So back then, what we did involve new physics and all sorts of heretical ideas, but turned out to be right. It really needed young and open minds to grasp and develop it further. Nelson and I later collaborated on calculating the normalized superfluid density at the transition point. We managed to come up with this universal jump prediction, where the ratio of the superfluid density is a universal constant in terms of various fundamental properties, e.g., mass of the helium atoms, Plank’s constant. And this is in principle a measurable quantity, because the superfluid density is basically the stiffness constant, to be measured by the flow properties.

Then there was still a slight problem to conquer. Superfluidity says that there's no dissipation in the flow, which implies that the flow velocity is finite. However, the theoretical prediction was at zero flow velocity and zero frequency. An extrapolation from the dynamical predictions was needed to agree perfectly with all the experimental measurements, which was later done by Nelson, Vinay Ambegaokar and B.I. Halperin. It took a few years for the physical community to accept that the weird theory (KT transition) was correct.

Q5: The KT transition has led to applications in superconductivity, superfluidity, and 2D materials, what’s your perspective towards them?

A5: The applications to superconductivity and related phenomena seemed natural. One could say that a superconductor is also a type of superfluid, and our theory should be applicable to it as well. The vortices are the essential excitations to consider in the superfluid and the vortex cores can be described as point particles in two dimensions, which interacts as Coulomb interactions. You can use the same vortex language for superconductivity except that the vortices in a superconducting film interact with a screened Coulomb interaction with a finite screening length.

Thouless and I published a paper predicting that there should be no phase transition in superconducting films. But it turned out that the screening length in a thin superconducting film is often so long—even bigger than the experimental system itself. Thus it's very nice to see that our theory of superfluid can also apply to some superconducting films. Similarly, for two-dimensional material whose penetration length is larger than its scale in one dimension, KT transition can also be applied to.

Thouless came up with all sorts of wonderful applications based on topological ideas.

The only frustrating part was that I had a health issue that kept me from participating for about six months. Since then, the KT transition has found applications across a wide range of systems, both quantum and classical.

Q6: Topological concepts are now widely used in physics, leading to promising applications of topological insulators and quantum computing, what’s your vision about them?

A6: David Thouless deserves more credit for introducing topological ideas into physics. But since I was involved in it, I suppose my name has become associated with it as well. My perspective on this is fairly simple-minded. In quantum computing, you need some sort of object to carry information, so these topological objects are especially useful because they’re not local—they spread and therefore less susceptible to local imperfections, which are inevitable in normal material. In my opinion, it was the key advantage of these topological materials.

Q7: Could you name the three most important unsolved questions in condensed matter physics?

A7: Prediction is not my advantage. I prefer to jump in and explore, and then you will naturally know what is important. One of the important unsolved questions to me is in driven out of equilibrium systems:

‘Consider a driven out of equilibrium system has a set of possible stationary states. Is any of the states unique?’

To answer this one, I think one need to include some stochastic noise into the system and to have it started. It eventually will come to a stage of one stationary state. Is there a stationary state unique or deterministic? Or does it depend on initial conditions? Such important question—tying with the evolution of life—may not seem a question to many. However to me, it is the ultimate question, and no other problems are of equal importance.

Q8: One of your remarkable achievements is to implement topology in physics, showcasing a paradigm of breaking the boundary of disciplines. Our journal eLight is targeting at expanding the boundary of optics and exploring cross-disciplinary research. What should be most valued, when exploring cross-disciplinary research? What kind of cross-disciplinary research could generate broad impact?

A8: I thought about such questions—but without any answers. The truth is, many major discoveries come out of the blue. Some strange and ridiculous ideas may eventually turn out to be relevant and correct. I don't believe anyone can predict which field or direction an important idea will come from—it could emerge from anywhere. So, don’t focus on making a broad impact while you’re doing research. When I was working on KT transition, I wasn’t aiming for Nobel Prize. I pursued it simply because it made sense to me. The idea of waking up one morning and saying, ‘Today, I’m going to do something worthy of a Nobel Prize’ would be nice, but that’s not how science works. There’s no way of telling what is going to be important. The only thing one can do is to conquer some problem that truly interests you. Have fun doing it and if you're lucky, it will turn out to be important with applications here and there.

Cross-discipline is of course important, and you should try to make people from other disciplines to understand your works. David R. Nelson understood me and tried to prepare an experiment, and I witnessed experiments I had never thought about. Cross-discipline can make theorists and experimentalists understand each other, and find the truth. No matter how fancy your theory is, the ultimate authority is whether the prediction of your theory can be verified or not.

Q9: Looking back, was there a defining moment or a crucial insight that helped you persist in your research despite early skepticism?

A9: What has mattered most to me wasn't a particular thought or idea—it was meeting the right people and finding the right problem to work on. My personal advice for overcoming skepticism is this: find a problem that genuinely excites you. Once you're excited, you're motivated, and that motivation will carry you through. If your work is sound and correct, the skepticism will eventually fade away.

Another key insight is to have fun with your research. That’s easier said than done, because if you are paid to do research, usually what you find fun is not what whoever paying you finds fun. Many people prioritize success over fun, but the unfortunate truth is, not many people actually achieve success. That’s why it’s important to let go of the pressure to be important or famous.

Instead, find a problem which turns you on, then dive in—without worrying about what others think. If you’re lucky, it might turn out to be important. And actually, I personally believe that if you’re genuinely having fun doing your research, you will get a better chance of being successful as well.

Q10: What advice would you give to younger generation interested in theoretical physics?

A10: Personally, I’ve been extremely lucky. My father was a well-known academic—brilliant with full of unconventional or even heretical ideas. He was also a determined person, firmly believing that his ideas were important and worth working on. This attitude infected me and my academic career was dedicated to trying to understand things. My advice to young generation, as through the whole conversation, is to ‘have fun’. You are pursuing a pathway to scientists. Scientists may not make the greatest living; to me, I enjoy it because I am paid to have fun.

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References

DOI

10.1186/s43593-025-00090-0

Original Source URL

https://doi.org/10.1186/s43593-025-00090-0

About eLight

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