Mike Stay has pointed out an interesting interview of Voevodsky, in Russian:

Here’s a bit of the first part in English, with a lot of help from Google Translate:

**Question:** The most famous result of yours is the solution of Milnor’s problem of K-functors of fields. You got it back in ‘96. And what happened next? How did your scientific interests evolve in the following years?

**Answer:** First, it was necessary to prove the generalization of the Milnor hypothesis, now known as the Bloch-Kato conjecture. The basic idea of this proof I formulated at the end of 96, at about the same time, when I wrote the first complete version of the proof of Milnor’s conjecture. In the approach that I came up with for the proof of Bloch-Kato, there were several problems. First, it depended on some “sub-hypothesis”, which was a generalization of a single result of Marcus Rost. Secondly, from the development of much more advanced concepts in the motivic homotopy theory than those that were sufficient to prove the hypothesis of Milnor. It was clear that Marcus could most likely finish the first one, and the second one I would have to do. As a result, the first was completed in, in my opinion, 2007 or 2008 by Suslin, Zhukhovitsky and Weibel, based on Marcus’s sketches. And I finished all the preliminary work and the proof itself only in February 2010.

It was very difficult. In fact, it was 10 years of technical work on a topic that did not interest me during the last 5 of these 10 years. Everything was done only through willpower.

Since the autumn of 1997, I already understood that my main contribution to the theory of motives and motivational cohomology was made. Since that time I have been very conscious and actively looking for. I was looking for a topic that I will deal with when I fulfill my obligations related to the Bloch-Kato hypothesis. I quickly realized that if I wanted to do something really serious, then I should make the most of my accumulated knowledge and skills in mathematics. On the other hand, seeing the trends in the development of mathematics as a science, I realized that the time is coming when the proof of yet another hypothesis will change little. That mathematics is on the verge of a crisis, or rather, two crises. The first is connected with the separation of “pure” and applied mathematics. It is clear that sooner or later there will be a question about why society should pay money to people who are engaged in things that do not have any practical applications. The second, less obvious, is connected with the complication of pure mathematics, which leads to the fact that, sooner or later, the articles will become too complicated for detailed verification and the process of accumulating undetected errors will begin. And since mathematics is a very deep science, in the sense that the results of one article usually depend on the results of many and many previous articles, this accumulation of errors for mathematics is very dangerous.

So, I decided, you need to try to do something that will help prevent these crises. In the first case, this meant that it was necessary to find an applied problem that required for its solution the methods of pure mathematics developed in recent years or even decades.

Since childhood I have been interested in natural sciences (physics, chemistry, biology), as well as in the theory of computer languages, and since 1997, I have read a lot on these topics, and even took several student and post-graduate courses. In fact, I “updated” and deepened the knowledge that had to a very large extent. All this time I was looking for that I recognized open problems that would be of interest to me and to which I could apply modern mathematics.

As a result, I chose, I now understand incorrectly, the problem of recovering the history of populations from their modern genetic composition. I took on this task for a total of about two years, and in the end, already by 2009, I realized that what I was inventing was useless. In my life, so far, it was, perhaps, the greatest scientific failure. A lot of work was invested in the project, which completely failed. Of course, there was some benefit, of course — I learned a lot of probability theory, which I knew badly, and also learned a lot about demography and demographic history.

In parallel, I was looking for approaches to the problem of accumulating errors in works on pure mathematics. It was clear that the only solution is to create a language in which mathematical proof can be written by people in such a form that it can be checked on a computer. Up until 2005, it seemed to me that this task is much more complicated than the task of historical genetics, which I was engaged in. In many respects this feeling was the result of an established and very widespread among mathematicians opinion that abstract mathematics can not be reasonably formalized so accurately that it is “understood” by the computer.

In 2005, I managed to formulate several ideas that unexpectedly opened up a new approach to one of the main problems in the foundations of modern mathematics. This problem can be formally formulated as a question of how to correctly formalize the intuitive understanding that “identical” mathematical objects have the same properties. Arguments based on this principle are very often used in modern mathematical proofs, but the existing foundations of mathematics (Zermelo-Fraenkel set theory) are completely unsuited for the formalization of such arguments.

I was very familiar with this problem and thought about it back in 1989, when Misha Kapranov and I worked on the theory of $n$-categories. Then it seemed to us that it was impossible to solve it. What I was able to understand in 2005, combining the ideas of homotopy theory (parts of modern topology) and type theory (parts of the modern theory of programming languages) was absolutely amazing, and opened up real possibilities for constructing the very language in which people can write proofs, which can check the computer. Further there was a big break in my mathematical activity. From June 2006 to November 2007 I did not do math at all. What happened during this period, we will discuss in another part of the interview. Now, thinking about that happening to me at this time, I often recall the story by A. and B. Strugatsky: A Billion Years Before the End of the World. I returned to mathematics at the end of 2007. I worked first at intervals, then on ideas related to historical genetics, then at the end of the cycle of work on the proof of the Bloch-Kato hypothesis. I returned to the ideas connected with the computer verification of evidence only in the summer of 2009, when it became finally clear to me that with historical genetics nothing happens. And just a few months later there were two events that advanced these ideas from general hints, which I thought I would have to work on for more than a year, to the stage at which I was able to state that I had come up with new foundations of mathematics that would solve the problem computer verification of evidence. Now this is called “univalent foundations of mathematics”, and it’s studied by both mathematicians and theorists of programming languages. I have almost no doubt that these foundations will soon replace the theory of sets and that the problem of the language of abstract mathematics that will be “understood” by computers can be considered basically solved.

## Re: Vladimir Voevodsky, June 4, 1966 - September 30, 2017

I felt Voevodsky to be one of the most profoundly individual and creative mathematicians of our time. My impression is that he was not at all interested in following trends or of filling in the details of a sketched picture, he was the kind of person who paved the way for others, whose mathematics had a very personal vision to it.

I was at the IHES birthday conference for Grothendieck in January 2009, where Voevodsky gave a really nice talk going through the proof of the Bloch-Kato conjectures, which he began with an announcement the formal completion of that proof. I was struck by how well he went through everything, including working out on the spot something he had forgotten some details of and under some questioning from Serre, despite his interests having been very much elsewhere for a number of years at that point.

I was very much interested in his work on motives at that time, and his work was extremely beautiful. He also had a great gift for exposition.

I also remember fondly a blog post of John Baez’s here where he linked to Voevodsky’s first note on the homotopy $\lambda$-calculus. The first time I looked at it, it was completely incomprehensible, it was just so far removed from anything I had even seen. Later, around 2009 I think, I took some further looks, and began to understand something, and began to program a bit in Coq, and I began to appreciate the beauty of what he was doing. I remember trying to get some people interested in it in Oxford at that time, and that point it was so new, none of the later work by people in what is now the HoTT community had appeared in print, and people’s reaction universally was that these ideas were so far out, they could not possibly understand them or think that they could be relevant any time soon. All that changed of course a few years later, when HoTT became rather fashionable. I still think, though, that Voevodsky’s first note on the homotopy $\lambda$-calculus outlines a beautiful vision, and that there are insights in it which may not be so easily gleaned from the HoTT literature.