In the first part of his research career, Michael Nielsen worked at the vanguard of quantum computing. His research on entangled quantum states, high dimensional curved spaces, and optical clusters have had a profound influence on the development of quantum information both in terms of bringing to fruition a scalable quantum computer, and for the value this research confers to fundamental physics. With Ike Chuang of MIT, Nielsen is the author of Quantum Computation and Quantum Information, a landmark publication that remains the standard text in the field and one of the most highly cited works in the history of physics.
A native of Australia, Nielsen came to the United States to work with Carl Caves (PhD '79) at the University of New Mexico. After an appointment at Los Alamos National Laboratory, Nielsen arrived at Caltech as a postdoctoral scholar in the two years prior to the creation of the Institute of Quantum Information. At the University of Queensland and then at Perimeter Institute, Nielsen continued to conduct pioneering research, and the whole of his research achievements include work in quantum gate teleportation and tomography. In 2007, Nielsen then took a dramatic shift in his career. As he explains below and has discussed elsewhere, quantum computation is not only a promising technology; it is also an important tool for framing how we think about cognition and the production of knowledge.
From that vantage point, Nielsen then threw his full effort into advocacy of open science, an initiative concerned with how scientific knowledge is shared - or how it should be shared by improving the systems and incentives that treat science as a common social good with its conferred knowledge shared openly and subjected to healthy competition and debate. In this field too, Nielsen has made profound contributions which have shaped scientific research, best practices in publication, and scientific policy. When faced with a question on possible breakthroughs that would compel him to return to quantum computer research, Nielsen sees this as unlikely, but acknowledges the element of surprise in scientific progress means that he can never say never.
DAVID ZIERLER: This is David Zierler, Director of the Caltech Heritage Project. It is Tuesday, October 11th, 2022. I'm delighted to be here with Dr. Michael Nielsen. Michael, it's so nice to be with you. Thank you for joining me today.
MICHAEL NIELSEN: Thank you so much, David.
ZIERLER: Michael, to start, would you please tell me your title and if you have any institutional affiliations besides all of the things that you run yourself?
NIELSEN: I am a Research Fellow at the Astera Institute, which is a not-for-profit research institute, mostly based in the Bay Area. I'm in San Francisco.
ZIERLER: What does that association do for you academically, socially, besides all the things that you do on your own?
NIELSEN: The Astera Institute was started a few years ago by Jed McCaleb, who was one of the early people involved in cryptocurrency - Jed created the Ripple and Stellar cryptocurrencies. Jed also has a very strong interest—in fact, now, I think it's his primary interest—in several kinds of research. He's particularly interested in artificial intelligence. But he started Astera as a way of supporting several types of basic research and, also, more applied research on the technology side. For the last few years, I've worked on what some people would call the science of science or metascience. It's an emerging research field, which is about studying and improving the social practices of science - all the institutions and customs and processes we use to support and enable scientists. The Astera Institute has a metascience arm, which aims to support this kind of work, so it's a very natural place for me to work.
ZIERLER: Michael, are you engaged in fundamental research currently, or that's really more from a previous aspect of your career?
NIELSEN: I would say I'm engaged in fundamental research currently. It's a little bit peculiar. Metascience is not really quite a field at this point! It has its origins in things like philosophy of science and history of science. Are those scientific fields or not? Not exactly. There's certainly a strong empirical element. People are interested in—just to give you some very basic examples—what sorts of funding schemes or approaches to granting are going to result in the best outcomes for science? In fact, even the question of what does "best outcomes" mean? Is it best for society as a whole? To what extent does that depend on the current situation of humanity as a whole? Those are very big picture things, all the way down to very local things: how do processes like granting and training and research culture affect individual scientists' career trajectories? How do they affect the kind of work that can get done? Are there bottlenecks preventing certain kinds of crucial work from occurring? Underlying are very fundamental questions about humanity: how humanity constructs knowledge, how we come to understand the world. I don't think you could describe metascience quite as a science at this point; maybe at some point in the decades to come. That's a theme of my entire career: I'm always interested in things as they're getting started. My original affiliation was doing quantum computing-style work, and now quantum computing's a very grown-up field with lots of people working on it. When I got interested back in 1992, there was just a tiny handful of people working on it. One of the most common questions back then, if I talked to other physicists about it, was, "Is this really science at all?" I could've been asked the same question at that time. "Is this really fundamental research?" I think that's quite a common theme, and maybe a personality characteristic.
ZIERLER: Michael, are you currently following advances in quantum information and quantum computing? Are you still in that research community?
NIELSEN: Mostly at the gossip level—
NIELSEN: —[laugh] meaning, various old friends. Just this morning, my friend Scott Aaronson asked whether or not we could have lunch tomorrow. It's at the level of just keeping up with old friends, and finding out what they're up to, sure. I am fascinated by the fact that, for so long, for [laugh] almost 30 years, quantum computing was viewed technologically as something in the distant future—and that is no longer true. Now, when I talk to friends in places like Google X or PsiQuantum and places like this, it is clearly becoming a technology that might actually have practical, real-world impacts. I don't know. Is it a few years away? Is it still decades away? I'm not sure about that. But it's much more serious as a technology than it was even, say, 10 years ago.
Surprises in Quantum Computation
ZIERLER: Given that you were part of that founding generation, what are you surprised of in terms of the timescale, where we are right now, relative to where the field started 20–25 years ago?
NIELSEN: I think I underestimated the extent to which small incremental progress was going to ultimately be the solution, and also, to some extent, borrowing from older existing technologies. Now, this sounds like an obvious point in retrospect—and it probably was obvious in advance to some people—but many trillions of dollars have been put into semiconductor manufacturing infrastructure. It turns out—it shouldn't surprise me but it did—it turns out to be just tremendously enabling. A lot of the current work which is most promising has just been finding ways of borrowing pieces of that infrastructure. The infrastructure alone is not enough, but it certainly helps to have that in the background. There's other things also. I don't think quite trillions of dollars has been spent developing lasers, but a lot of money has been spent developing very, very good laser systems. There's all this industrial base which we've developed, and so as more and more of that has been put into quantum computing, you just get a lot of stuff for free. I didn't really appreciate the extent to which that was going to help particularly with the scaling problems, making large-scale systems.
ZIERLER: Michael, was there a dramatic moment in your life when you decided to pivot toward all the things you're doing now? If we can call you perhaps a public intellectual in the scientific realm, did that happen at a sudden moment? Was it a slow burn? How did that all come about for you?
NIELSEN: Much like quantum computing, it was slow then sudden.
ZIERLER: [laugh] That's good.
NIELSEN: There's really two fundamental choices I made. One, very early on in my life, there was a question: do I become a scientist conventionally construed, which for me was always likely to mean theoretical physics, or do I go into computing? That's been a question in my life since I was a teenager. It was a little bit of an accident that I went into theoretical physics first. I'm guessing what you're pointing at, because you know a little bit about my history, I made a choice in 2007 to leave a tenured research position at the Perimeter Institute in Waterloo, in order to go in a very different direction. Viewed as a one-off decision that looks a very sharp discontinuity. As a personal intellectual decision, it was a natural outcome of things which had been brewing for years.
ZIERLER: I wonder if the term "natural philosopher" resonates with you in the—
ZIERLER: —19th century, for example, the idea that there was this strong divide between intellectual pursuits and science isn't nearly as demarcated as it is right now.
NIELSEN: The reason we get sharply demarcated fields is, of course, because we make progress. Maxwell understood how electromagnetism works: now you've got this deep set of insights, you can erect a social structure around it. You can start to build institutions around it. To some extent, the boundary around the discipline of physics today is partially because of that. Such boundaries are not arbitrary. Even though there's just one world, we do have multiple core nuclei of understanding, and different cores result in different disciplines. You're a historian: there are, of course, deep practices which historians master, which are just not obvious at all from the outside. I know when I read history or history of science, while it's interesting and I can follow, I don't understand all the deep practices in the background, making it tick. For all these reasons I reject the fashionable idea that these demarcations between fields are arbitrary or mostly contingent. On the other hand, the demarcations also tend to lag actual intellectual development. Basically, our social institutions can't adapt. They're slow to respond to intellectual currents. The kinds of subjects I tend to be interested in are often things where institutions haven't yet had time to get invested. That hasn't changed. When I was interested in quantum computing very early on, one of the most frequent questions I would get from physicists was, "Is this even physics?" That's not a question that would be asked today, but it was certainly a question that I was asked an awful lot in the 1990s. That's just one example of where there's this lag between institutions' and communities' ability to absorb new ideas, where ideas are actually at. That's a long-winded way of saying I tend to like those things which are a little bit illegible to existing institutions. That's where I'm most comfortable, just for personality reasons. I haven't consciously intellectually chosen this. It's just who I am.
ZIERLER: Michael, I'm curious, just a chronology question, did your interest in the open science movement, at least in its modern incantation, did that develop in parallel with your interest in quantum computing, or was it more sequential; one came after the other?
NIELSEN: Well, one came after the other but probably not in the direction you would guess. I was interested in open science in the late 1980s, so as a teenager. There were a few things I read that were very important. Alvin Toffler wrote these books, The Third Wave, and Future Shock, which I read as a teenager, and much of the theme of those books—he was a consultant, I think, at AT&T or one of the big telecommunications companies -- somehow, he had realized that the internet was going to matter a lot for how we construct knowledge. He was one of the first people to really understand that the internet was going to reorganize society in a whole lot of ways. What was particularly striking to me at the time was the notion that it was going to change the way in which we construct knowledge, by changing the coordination structures that we use. Then, also, there's this parallel theme which is that ideas around computation and artificial intelligence are also going to change the way we make discoveries. I thought this was just fascinating as a teenager. I didn't quite know what to do with it. Later, part of the reason I got interested in quantum computation was because of this. I read this wonderful paper by David Deutsch where he effectively asked the question, "What is a computer anyway? How does this notion originate in nature?" I was so interested in computers and what they do, this question just seemed absolutely fascinating to me. In that sense, my interest in open science pre-dates my interest in quantum computing, and actually helped to cause it.
Connecting Quantum Information and Open Science
ZIERLER: How do you see specifically intellectually your interest in open science influenced the kinds of questions you wanted to pursue in quantum information theory?
NIELSEN: Like a lot of researchers, particularly young researchers, I was very pragmatic. I didn't really know what I was doing. The field of quantum computing and quantum information was developing very rapidly at the time. I entered it in the early to mid-1990s. There were a lot of low-hanging fruit, and you just look around, pragmatically, and say, "Oh, there's this problem over here, which I could do something about," and so I would work on that. I worked on quantum process tomography, figuring out how to determine quantum processes experimentally, with Ike Chuang. I worked on quantum gate teleportation, also with Ike. These were not things that were premeditated. We saw an opportunity, but there was no guiding philosophy. It was just a very pragmatic thing. There was the opportunity there, we seized it, and hopefully did something useful. Later on, I started to change the way in which I work so it's more guided by something more principled and long-term.
ZIERLER: The term "open science movement" suggests a level of cohesion. Is that fair? Is there an actual community? Is it more amorphous than that? How do you see this?
NIELSEN: It is certainly more amorphous. Years ago, I saw a reference to the term "open science" being used sometime in the 1600s, I believe, by Boyle or by Hooke. At the time, I thought, "Oh, that's interesting." I've never been able to re-find the reference, which frustrates me immensely. Speaking of what historians are able to do, they're just incredible at tracking down this kind of stuff. In the modern era, there are references to open science starting in the 1970s and 1980s. But I think the first person to really figure it out as something where there's a modern possibility for action was the economic historian Paul David, at Stanford, who wrote a beautiful paper about the history of open science. He wrote it over a period of about 20 years. I think the earliest drafts appear around 1990 or 1991, and the final draft appears in 2010 or so. He was writing a history of what he saw as the first open science revolution back in the 1600s, when people like Henry Oldenburg and others were realizing that there was a value in developing a political economy for science with scientists rewarded for openly disclosing their results. David realized that this was a major transition in the history of humanity, bringing the printing press and science together in one unified institution.
Following David, a bunch of people realized that there was a similar opportunity today around open online sharing of papers and also code and data and various other things. People have realized this from very different points of view. There are people, particularly in social psychology, who got interested in open science from the point of view of making results in their discipline reliable. Then there are people in areas like particle physics or astronomy, who are perhaps mostly interested in it because they're able to share data more broadly. Something like the Sloan Digital Sky Survey, they get enormous value out of making their data publicly available. There's been these parallel tracks where different communities have come to very similar ideas more or less independently, and so there's some cohesion—to answer your question—but there's also these people doing things very separately as well, sometimes unaware of each other. I think over the next 20 or 30 years, that will continue. There will be people doing their own thing but there will also be gradually increasing cohesion, particularly at the government level.
ZIERLER: Michael, all of your work in deep learning and artificial intelligence, would you say that you come to these issues with a specific quantum perspective in mind, or is that a separate pursuit?
NIELSEN: That work on deep learning is just a hobby, albeit a fairly serious hobby. I'm interested in it for similar reasons to my other work, though, which is I'm very interested in the systems which humans use to support discovery and creativity. That's a unifying theme behind most professional things I do. But people sometimes assume I've done a lot of work on deep learning, and I'm a little embarrassed by that: I haven't. I accidentally wrote a book about it, which creates a certain impression of seriousness of intent. What happened was I got a group of friends together to talk about deep learning. I gave some short lectures. I started to write some notes, and they gradually metamorphosed into a book. But I wasn't intending to do serious research there.
ZIERLER: Now, to the extent that it's just a hobby but one that you think a lot about, what's the state of play in AI right now? What are the things that are most interesting to you?
NIELSEN: It's a hard question to answer. There's a great letter from Wolfgang Pauli to a friend in 1925 or '24, when quantum mechanics was being invented. He said that he felt very confused, and it was very difficult to understand what was going on, and he wished he'd been a plumber or a playwright or something like this. AI, at the moment, has a very similar and interesting feeling to it where, locally, there's a tremendous amount happening. I think the really big thing that has been realized over the last few years, it used to be that you needed a lot of what's called labeled training data to train AI systems. If you wanted to train it to recognize cats versus dogs in images, you would get thousands of photos of cats and dogs, you would hire some people to put labels on them, saying whether they were cats or dogs, and you would train your system. They've figured out how to do this kind of thing without having the labels, so just having the raw data as human beings do. The world is not labeled for our convenience. We're able to pick things up anyway.
This kind of unsupervised learning, people have figured out how to make it work in the last few years, and they've figured out how to make it work in a remarkable way. I'll just describe it, if you don't mind, in the context of the language models. The idea is to take an enormous amount of text, millions of web pages, for example, and train a system whose only job is, given a sentence up to some point, is to predict the next word in the sentence. If you take enough computing power and a complicated enough model, it turns out we can actually train it to do this pretty well. You can just do this using data collected in the world. There's no need for any labeling procedure. That doesn't sound like a very useful thing to be able to do! It turns out, however, that if you do this, and then you start to prompt this system just with pretty simple prompts, so you can say to it, "I'd like a paragraph in the style of the Old Testament," the next predicted words actually turn out to be, remarkably enough, in the style of the Old Testament! You can do this for a large number of different tasks. A long-time dream in AI has been what they call transfer learning, where you learn how to do one task, and then it's able to do other things. If it's a language system, it can figure out whether something is a noun or a verb. It can figure out what the subject of a sentence is. It can figure out all these other things. Transfer learning has never really worked terribly well, up until we started training these foundation models just a few years ago. All of a sudden, it turns out these systems trained unsupervised to do prediction are also able to do this transfer learning: they're being trained on just one very simple task, and it turns out it can do hundreds of other tasks remarkably well, better than the state-of-the-art specialized systems beforehand. Those two advances really shocked me. A lot of the stuff that you see in the news about advances in AI are really being driven by those two things in particular. There's a lot of low-hanging fruit, I think, still to be picked there, and I don't know just how far we'll get. It's a very exciting time. That was a very long answer.
ZIERLER: No, that's great. In reflecting on your excitement in the 1990s about what the internet could do, what has aged well and what hasn't in terms of where we are today with the internet?
NIELSEN: I forget who was asked what they thought of the French Revolution, and replied that it was too soon to tell—
ZIERLER: Right, sure. [laugh]
NIELSEN: —170 years after the fact. I think that's certainly true. Depending on what you count, the internet is maybe 50-odd years old. What would you have said about the printing press or the alphabet or writing 50 years after their invention? I think it really is too soon to tell. Obviously, there's some pretty strange things around social media, what it does to governance, and how we relate to what our systems for disseminating information and truth are. I don't know. I tend to be just very optimistic in general, so I'm optimistic that we will eventually figure those things out. But, at the moment, there are some significant issues. I'm not sure how to make sense of the question, David, without it being narrower.
ZIERLER: It's worth it, though? The internet has been worth it, in your view, so far, at least?
NIELSEN: Yeah, I think very clearly so. Just to pick one example, I think it's tempting to look at something like COVID, and think, "Wow, lots of misinformation was spread around about COVID," and so on and so forth. But I don't think that we would've had the same kind of coordinated response very early on if it hadn't been for the internet. If you look back at the Spanish Flu in 1918, a lot of news was suppressed around that. Indeed, part of the reason, I am told, why it's often called the Spanish Flu isn't because it originated in Spain. It's actually because the Spanish authorities were more open than authorities in a lot of other countries. Authorities in a lot of other countries would suppress the news about the flu, and so it sounded like it was coming out of Spain. I don't know whether the story is true or not, but it's at least plausible. That kind of information suppression strategy is, I think, much harder to do now. It's just much easier for people to collectively realize, "Oh, this is a really big deal. We need to respond to it. Staying home for a while is maybe a good idea to the extent we can manage it." Even though you then have all these problems with making decisions about vaccines and Paxlovid and things like that, I think what we initially bought was very well worth it.
Open Science and Public Communication
ZIERLER: Michael, because you can reach a much larger audience in the current incarnation of your career than you could in academia, what are some of the real pleasures of that in being able to talk to just a much wider, more diverse group of people, and sharing the things that are important to you?
NIELSEN: Academics can also do that if they choose to. Certainly, the choice to focus on very fundamental questions at very early stages of development often means that I can write in a way that's reasonably broadly accessible, and it's fun, partially, just because it brings me into contact with a more diverse range of people. I enjoy that a lot. When you meet somebody who has a very different background but one with a lot of depth, it's just immensely enjoyable to get a little slice of that. A friend of mine who writes popular books about physics was once asked why he did that. I expected the answer would be a conventional one, something about educating the public or similar. He didn't give that answer at all. He gave a much more interesting answer, which was he drew a big circle, and said that he felt that, intellectually, most people, they're well inside the circle, they're not trying to push out the boundaries of human knowledge. But there are a few people in many different disciplines who are pushing out those boundaries. There's some physicists over here on one boundary. There's some artists over here on some other boundary. There's people pushing elsewhere, thinking about law and so on. The reason why he wrote popular books is because he wanted to be able to connect to people in those different areas - people who are pushing the boundary of thinking about law, people who are pushing art, people who are pushing music, people who are pushing all these different things. I really resonated with that, and I really enjoy that opportunity to meet people who are just thinking seriously about things that I know nothing about.
ZIERLER: Michael, when you decided to pursue advocating for open science, really, as a full-time vocation, what did you learn about the most effective institutional partners: government, industry, academia? Who did you need to join forces with to push these ideas forward?
NIELSEN: It turns out, as a full-time advocate for open science for five years, I don't think I was very good at it. I don't have quite the right personality for it. I'm much more interested in ideas than I am in advocacy fundamentally. I like doing synthesis work. I like doing analysis work. The kind of coalition building and partnership building that is very effective in pushing a movement is not something which is my natural métier in quite the same way. Heather Joseph is a really good example of somebody who's just been incredibly effective at doing that kind of thing, and she's had a lot of impact at the policy level.
To the extent that I was able to help with that, it's by doing intellectual work in the background that then, hopefully, informs what some of the people who are actually working directly with government and so on, are working on. I did find a certain amount of enjoyment and, hopefully, efficacy in working directly with people at the science publishers. Mostly that's just conversation backwards and forwards. They're thinking about how they change their platform, what they do, what policies they adopt going forward, and just having a lot of conversations with those people. Sometimes, it was very formal. I would come in, and give some talks or whatever. But a lot of it was just informal conversations over the years. Those publishers get a lot of criticism, some of it deserved and some of it undeserved, but they've really changed their position a lot over the last 20–25 years. The thing that I think is very hopeful is people trying to develop new tools and new businesses. That is something I particularly enjoyed, just chatting with people who are trying to get those kinds of efforts off the ground. It's difficult for me to say to what extent I really helped. Even just being a sounding board though is sometimes useful.
ZIERLER: Michael, going back to 2008, in making this career switch, what were some of the biggest risks that you saw at the time, everything from intellectual to financial?
NIELSEN: [laugh] I had no idea how I was going to get paid. I moved from this notionally tenured research position at Perimeter Institute to having no idea what I was going to do financially. There was just a certain amount of living off savings and very small gigs for some number of years. That was scary. I should put that in context: a lot of people do a lot of things which are far more scary than that. I have immense admiration for police officers or fire fighters or the military or whatnot. They're doing seriously scary things. But, in its own way, my choice was a challenge. Intellectually, this is, I think, an issue for anybody who does creative work, if you really know how it's going to come out, you're probably not being daring enough. I had gone from working on this research program, doing quantum computing which, by that time, was quite a respectable subject, and I felt very in control of that in a lot of ways, to doing this work which was partially advocacy and partially just intellectual development of a set of ideas around open science. I had no idea how that was going to come out.
There were people doing adjacent work on open access and open data. But I don't think there was anybody else in the world who full-time was just working on open science, broadly construed, at the time. That was scary intellectually. There's this sense of going a long way out on a limb, where I didn't know: was this just a waste of time? Is this going to turn out to be a bad idea, in retrospect, or was there something really there? But I also have the sense that that is intrinsically always the case with any creative work worth doing. If it has a very strong community context, a very strong institutional context, almost by definition, you're working within an existing consensus. Once you place yourself outside that consensus, it is intellectually a little bit frightening. You're certainly much more likely to make bad mistakes, and I think I did make some bad mistakes. But I think it's also essential to make a more significant marginal contribution.
ZIERLER: Michael, two current questions before we go back and develop your personal history. First, just as a snapshot in time, circa October 2022, what are you working on these days? What's interesting to you?
NIELSEN: I'm just finishing a short book with a friend and colleague Kanjun Qiu. It's really just to sort out in our minds what metascience is about. In particular, we're interested in the question of how do scientific institutions change? How does the collection of customs and social practices, which are used collectively by all the institutions in our discovery ecosystem, how do those change over time? Is it possible to make them change and upgrade more rapidly? You think about things like, say, the NIH, the National Institutes of Health, panel system for awarding grants. That has really not changed very much in many decades. If you thought that that panel system was perfect, maybe that's a good outcome. Maybe it shouldn't change. But talking to people who live under it and, in some cases are notionally in charge of it, I don't think any of them think that's true. Rather, it's a badly suboptimal system which doesn't seem able to upgrade itself. We just got very interested in this question of whether or not there are instances where it's possible to change those institutions so that they can really improve themselves. That's what the book is about. Hopefully, we're a couple of months away from finishing it. [laugh]
NIELSEN: We'll see.
ZIERLER: Michael, I wonder if you've had a chance to reflect on the recent naming for the Nobel Prize, which recognizes, perhaps more than anything else, these revolutions in quantum entanglement and, specifically, the origin story between quantum entanglement and quantum information theory. I wonder if you've thought about these connections, and what it might mean in broad historical perspective.
NIELSEN: My undergraduate thesis was about this stuff, very literally, the Bell inequalities, which is what John Clauser, Alain Aspect, and Anton Zeilinger have just won the Nobel Prize for - the experiments confirming that the real world, as does quantum mechanics, violates these Bell inequalities. I think it's Henry Stapp who described the Bell inequalities as the most profound result of science. I'm not sure I'd go quite that far but it's up there. It's just an incredible set of results. Bell realized that our notion of what reality is, is, in some deep sense, inadequate. That was a theoretical insight, which then the people who won the Nobel actually did the experiments to test. Of course, I have just the utmost regard for both experimental and theoretical sets of work. It's almost intimidating to say what it means. You almost feel too small before it. These are questions which are so profound that the mind or my mind reels before them. It's very tempting, I think, to jump to quantum technology, and say, "Well, these results have a certain kind of impact in the form of quantum computers." It's true that quantum computers are out of that intellectual lineage, in some sense. But our day-to-day technology is small potatoes compared to that change in what we think the universe is.
ZIERLER: Well, let's now go back. The fact that in the early 1990s, you were already thinking about quantum computers, even before many of the people that we consider founders of the field, that makes me wonder how far back were you thinking about these things. For example, in the '80s, when Feynman was talking about combining computers and quantum mechanics, were you alive to that? Were your antennae up to those kinds of ideas?
NIELSEN: I think when Feynman was doing that, I was 7 or 8—
NIELSEN: —and much more interested in playing soccer, actually, and somewhat interested in science but not yet in quantum physics. Now, actually, I can tell you what happened. In 1992, I was 18 and I was taking my first quantum mechanics class with Gerard Milburn, who's a professor at the University of Queensland. Gerard was the first person I met who in some deep sense is a scientist. That's the way he approaches the world. He'd be giving this sophomore class about quantum mechanics, and some of it is just standard sophomore stuff. But, because of the way he thinks, his mind is constantly engaged. One minute, you'd be getting the standard second-year explanation of the wave function, and then Gerard would, all of a sudden, be talking about—I don't know—some connection to Michael Berry's work on the Berry phase or something like that, so something very current, because his mind was so engaged with the research. Anyway, I just thought that this was an absolutely marvelous class. One day after class, it would've been two or three weeks in, I very shyly approached him, and asked if he had any suggestions for reading I could do on top of what we were covering in class. He told me to come and see him a couple days hence, and he would give me some papers. Anyway, I went to his office a couple of days after that. I was terrified. He had a sign up on his door. It was a little comic strip, I think. The punch line was a quote from the physicist Pyotr Kapitsa, a Nobel Prizewinning physicist, saying that the most important duty of a researcher was to their students. I saw this little quotation, and I was very encouraged by this, that I wasn't going to be wasting his time. I opened the door, and he gave me, I think, it must have been 500 or 1,000 pages of photocopied papers, which included David Deutsch's paper about quantum computing, Richard Feynman's paper about quantum computing, Charlie Bennett's paper about reversible computing, and a bunch of others. Now, this is 1992, so this is a long time before any of this stuff is fashionable at all. Gerard just told me that it was going to be very important. I spent a lot of time with that pile of papers. Particularly Deutsch's paper, I think, is a very interesting set of questions about what knowledge is, about how the universe makes sense of itself in some sense. Those are not the terms he [Deutsch] would necessarily use, but that was some of the sense that I got at the time. I just thought it was absolutely wonderful.
ZIERLER: A question that you've thought about a lot then and since is this idea that is quantum information physics. What was your intellectual framework? How did you root quantum information in the way that, for example, John Preskill got to this by cosmology? What was your foundation point getting into quantum information theory?
NIELSEN: I think I was so ignorant at that point that there wasn't really a strong foundation in anything. John was a world-class cosmologist and particle physicist at the time. He got into it, so he had this strong established base of things which he understood. I was an 18 year old, and of course had a vastly weaker base. Of course, there were these very profound ideas around computer science and around quantum mechanics, which you can try and build off, and that became the kind of thing that I was interested in, in trying to assimilate some of the existing understanding, so understanding things like the Bell inequalities. In 1992, also, I had read Turing's 1936 paper, which is really the foundation of modern computer science. That's just a wonderful paper which, again, like Deutsch's paper, contains these really fundamental sets of questions. I felt like that was part of my growing understanding of the world but, also, just a set of questions that I wanted to understand the answers to.
From Australia to New Mexico
ZIERLER: Michael, when did you first learn of Carl Caves, and what made you so fascinated by what he was doing?
NIELSEN: That was just, I think, a couple of years later. When I was a freshman, I happened to chat with a couple of the math tutors who were going to Oxford to do PhDs. I started to understand a little bit about what was involved in leaving Australia and going elsewhere. I'm afraid, I knew at the time—and it is probably still true to some extent—the most interesting intellectual action is unfortunately elsewhere [than Australia]. A few years later, I was chatting with Gerard Milburn in my fourth year. "Where should I go if I wanted to pursue these ideas about quantum computing and quantum information and related ideas?" Gerard said, "You should go to the University of New Mexico, and work with Carl Caves." I didn't know anything really at the time. In retrospect, I can see there were probably three or four places in the world that would've been great places to go and, he was right, UNM was definitely one of them.
ZIERLER: What was Carl working on when you first arrived?
NIELSEN: I think much of his heart at the time, and maybe even still now, is actually in quantum chaos. The work he was doing was trying to understand what sensitive dependence on initial conditions means in quantum systems. That was of some interest to me at the time, though it ultimately wasn't what I wanted to do. But Carl had also created a group, which was working on a very wide range of questions related to quantum information and quantum computing. People like Chris Fuchs and Howard Barnum were working on some quantum information questions but also then some more fundamental questions about what the quantum state is, and what quantum mechanics means. Ben Schumacher was there: he was visiting on sabbatical, I think it was half a day a week. Ben is the person who originated the term "qubit," he proved the quantum noiseless channel coding theorem, and did a whole lot of other fundamental work in quantum information in especially the early 1990s. I got very interested in a lot of the questions that Ben was interested in, around what quantum information is, how we can protect it, these kind of questions. That, for me, was very exciting. Then the group as a whole supported this kind of work.
ZIERLER: Now, was Carl essentially a one-man show at New Mexico at this point? Was there a larger group like what ultimately would happen with IQI?
NIELSEN: When I arrived, Ivan Deutsch had just arrived as an assistant professor at the same time. Ivan, at that point, was interested in quantum information but I think he would've called himself more an atomic molecular optical physicist. He started then to gradually work a little bit with Carl and others. That took some time. Ivan was just reorienting himself. He was also living the life of an assistant professor, which is pretty tough, trying to round up students and do all that kind of thing. But Carl had been there for a few years, and was really the established presence in quantum information and quantum computing at UNM.
ZIERLER: What was your sense of the frontier in quantum information when you were a graduate student, and how might that have affected the kinds of topics you wanted to work on for your dissertation?
NIELSEN: That was the reason why, for me, it was so helpful to have Ben. He had a very specific sense of the frontier, which I resonated with personally. For him, that was about developing ideas - well, I shouldn't speak for him - but my interpretation is that it was about developing ideas from information theory as applied to quantum mechanics, so questions about resource conversion, and efficiency, and protection from noise. Let me back up a bit. Probably the most exciting thing, overall, was the set of ideas developed around protecting quantum systems from noise, so what we would now call quantum error correction and quantum fault tolerance, although those weren't terms in 1995.
Most physicists - certainly I - were shocked at the idea that it's possible to protect quantum systems from the effects of noise. Quantum states are these very delicate, apparently very analog things. It seems as though, if you have the slightest disturbance from outside, your atom is slightly impinged by a photon, surely it's going to mess the quantum state up just terribly, and there's no obvious way to protect against that. A whole lot of people, perhaps most crucially Peter Shor, but a large group of people figured out between about 1995 and 1997 that that conventional point of view was just wrong, and they figured out a set of techniques, quantum error correction and quantum fault tolerance, that will let you protect against such noise. From a practical point of view, that's important. It will be crucial to building or likely be crucial to building quantum computers. I think from a more fundamental point of view, it caused a rethink of how we think about quantum mechanics, and a realization that some of the prejudices or intuitions that people have are just wrong. I didn't really understand that very well certainly in 1995. In retrospect, that's the gravitational force which was gradually drawing me. More and more of my work as time went on was being influenced by these ideas about protecting systems from noise.
ZIERLER: What were the key conclusions of your thesis?
NIELSEN: The title is this very broad one: Quantum Information Theory.
ZIERLER: Were you asserting with the title that that was a thing?
NIELSEN: Oh, yeah, although that's not my assertion. Carl and Ben are two of the people, I think, really responsible for asserting that. They're not the only ones but [they had] some notion that this was true. Then Carl had two PhD students actually graduate in the same year, myself and Howard Barnum. I think we both had the same title for our dissertation. It's a little bit of a grab bag. I'd just spent three years working on this, and I think the intellectual circumstances of the time were very much—for me it was a grab bag. It was let's find a collection of related problems that I can solve. I can name a few. Gosh, it's been a while since I've thought about it. It's funny, the things that I'm proudest of, in retrospect, seemed very small at the time. I'm very pleased, for instance, with the work on quantum gate teleportation that I did with Ike Chuang. It was almost an accident. It was one of these side projects that didn't seem very important, and we almost didn't write up a publication.
But then, later, Ike and Daniel Gottesman developed the idea further, and then Manny Knill, Ray Laflamme, and Gerard Milburn developed it further, and now this idea is very important. But it was just a side issue at the time. It was something Ike and I accidentally discovered one day. I think Ike found it accidentally numerically using MATLAB, or something like that, and didn't understand the result. Then I provided a theoretical explanation, if I remember correctly, of why this quantum gate teleportation idea was working. But, now, this is something which people learn. Companies like—what is it?—PsiQuantum, it's in their DNA in some way. But there was no grand plan there. It's just something that happened. I think it was not really until later in my postdoc and, to some extent, even later still that I was pursuing a deliberate research program with goals and something a little bit more systematic.
ZIERLER: Now, this happenstance idea that you developed with Ike, is that essentially the origin story of the text?
NIELSEN: Oh, no, not at all. There was a six-month workshop run in Santa Barbara in the second half of 1996, which I think is actually very important for the field. There weren't many people working in the area at the time, and almost everybody in the field came through that workshop at some point. The two people who spent the longest there were me and Ike. We just had [laugh] a large number of lunches together, and we started working on various things. There was this idea of, as I mentioned before, quantum process tomography, this idea of quantum gate teleportation. I think we wrote one or two other papers as well. But I had been thinking, probably for a year or two at that point, just toying with the idea of writing a textbook. Ike was just finishing his thesis, and he submitted his thesis at Stanford in, I think, December of 1996. An editor from Cambridge University Press happened to be visiting Stanford, somebody passed him Ike's thesis, and he said to Ike—this is Simon Capelin, the editor—"Do you want to turn this into a book?" I happened to be visiting Ike a day or two later, and we were standing in the Borders bookstore there. Ike said, "Do you want to write a book together on quantum computing?" I said, "Sure, that'd be great." I didn't quite realize how much work it was going to be. [laugh]
ZIERLER: I'll fast forward in the narrative a little bit but, staying on the topic of the book, what is your sense of why it has been such a smash success? What about it resonates with so many people?
NIELSEN: [laugh] It is true, it has been successful. I think we're at about 50,000 citations for it now. There's an awfully large amount of luck, of course. We happened to write the right book at the right time. I suspect if we'd written the book two years earlier, it would've been the wrong book at the wrong time. A lot of basic ideas of the field came into a relatively mature state of development in the mid-to-late 1990s, and that happened to be when we were writing the book. When you get a lot of those foundations right, it's just natural then for people later to want to refer back to that text. Otherwise, I don't know. We put a lot of work into it. Something in my mind, and I think to some extent Ike's, we were both very oriented towards this broad synthetic view, and that's just a good orientation to have if you're trying to write something for that kind of audience.
ZIERLER: How much of an established field, circa late 1990s, would you consider quantum information theory? In other words, were there faculty positions that were advertising as such? Were there postdocs specifically oriented toward this? What did the field look like at that point?
NIELSEN: It was very, very challenging for people, particularly in the United States but, to some extent, elsewhere to get things like faculty positions. This is an example of what I was talking about before: intellectually, quantum information had the heft of a real field by this point. But the institutions hadn't caught up. If you wanted to get an NSF grant or something like that, it was very, very challenging to do so. They were a little bit unaware. There were some [institutions] which were aware. Things like—what's his name?—George Basbas, an editor of Physical Review. He realized that this field was going to be important and, all of a sudden, you start to see papers showing up in the Physical Review, and he deserves a lot of credit for that. But there's also a lot of institutional gatekeeping where people took a lot longer to realize what was happening. It's just extraordinary to realize somebody like Daniel Gottesman or Andrew Doherty or people like that were having trouble getting jobs. They probably can't walk five meters these days without getting a job offer. But the relevant institutions hadn't really caught up and adapted to the fact that this very exciting thing was happening. I think "grim" is a good description of the job market at that time.
ZIERLER: To what extent did Caltech loom large when you were a graduate student in New Mexico? Were you aware that, for example, John Preskill was starting to think about these things right at the same time?
NIELSEN: In 1997, Ben Schumacher went off to Torino to a conference there, came back. It was almost the only conference in the field at the time. No, 1996, it was 1996. Came back. I said, "How was it? What was good?" He said, "Oh, I met this guy, John Preskill. He's absolutely amazing. He's read all of the papers, and he can explain even your own papers to you much better than you understand them yourself." That's not a bad description of John. That was, I think, the first time I was aware of John. I knew, certainly, at Caltech, Carl is a Caltech person. He very greatly admires both John and Jeff Kimble. He certainly had spoken very highly of Jeff's work on squeezed states. But I didn't know that John was working on quantum information until that point in the middle of 1996, and then just gradually becoming aware. I think, particularly, John's student Daniel Gottesman wrote these very interesting papers about quantum error correction, probably late 1996, if I remember correctly, developing what we now call the stabilizer formalism. These are very exciting papers; really seminal work. Over the ensuing years, John and his group were a fount of ideas about fault tolerance, in particular, and then other fundamental ideas in quantum computing. It was a slowly dawning awareness on my part.
Caltech Before the IQI
ZIERLER: What were the points of connection that led to your postdoc at Caltech? Did you talk about this with John? Was that Carl's advice? How did that work?
NIELSEN: When I was in Santa Barbara in late 1996, with the effrontery of youth, I just emailed John out of the blue, and said, "Hey, I'm giving a talk here. Do you want to come along?" [laugh]—which he did. But then later that day, Ike and I got in the car, and went back to Caltech, and we got a lab tour from Kimble, and chatted with Hideo Mabuchi and with Daniel Gottesman and some others. That was my first time at Caltech. John emailed Carl, I think, shortly after that to say, "Michael should come and spend a month out here next summer." When I came out at the end of that, I asked John if I could come back for a postdoc. I had a nice time. It's a great intellectual atmosphere. Of course, Southern California is a wonderful place as well. I was delighted to come back.
ZIERLER: Tell me about your initial impressions when you arrived at Caltech. What do you remember?
NIELSEN: It's very small. I was expecting this gigantic place. It's very quiet. Something I really enjoyed [laugh]—I don't know whether it's really fashionable to say this—but [laugh] I do enjoy just how hard people at Caltech work. They're very, very serious about what they do—probably a little bit more serious in some ways than I was. Oh, that's not true. I was probably too serious in some ways. There is, I think, a self-conscious sense of really working to advance human knowledge that pervades the Caltech campus in a way that I find very buoying. It's sometimes intimidating and can make it hard to work. But a lot of the time, it's very buoying and makes it very easy to work because you feel like you're part of something important. It's just tremendous, and it's one of the things that makes Caltech very, very valuable.
ZIERLER: What was John working on at that moment?
NIELSEN: He was thinking about error correction and about fault tolerance. To some extent, he was also thinking about connections between that and his previous home in high-energy physics, and cosmology, and associated areas, whether there are any connections between things like the black hole information paradox and quantum information. I didn't understand most of what he was saying, but it just had the smell of something that was very important. Now, people would point to his papers on that subject with people like Patrick Hayden a decade or so later. But I think he already had that sense at that point, that there was something important there a long, long time before anybody else, I think, more than a decade ahead of almost anybody else.
ZIERLER: Michael, you arrived at Caltech before the formal creation of the IQI. What did that mean? What did it mean to be working in quantum information before the institute even came into being?
NIELSEN: Can you clarify the question? What do you mean?
ZIERLER: To the extent that the Institute, you know, the purpose of it is that it's bringing people together. Did you feel like you were working in a place that needed the institutional imprimatur? Was the fact that you were there part of the origin story of the IQI?
NIELSEN: I think from my point of view, it was already this terrific intellectual environment. Chris Fuchs was there. Kitaev came to visit for a bit. Peter Shor came to visit for a bit. Just a terrific group of visitors and people coming through. I didn't have any sense at all of a lack of institutional imprimatur. I don't know, of course, what was going on at higher levels—goodness knows, there's often a lack of office space and so on for such efforts, and maybe that was important behind the scenes; I don't know. But, from my point of view, being able to just knock on a door, and chat with Chris Fuchs or Hideo Mabuchi or, for that matter, John—John was in a different building, which was maybe a little unfortunate—that's just terrific.
ZIERLER: Were you involved at all with the discussions that led to the IQI? Were you at least aware that they were happening?
NIELSEN: [laugh] Not really. I was a postdoc, so you're at this very low institutional level. The institute is not consulting you on those kinds of things. I think it was probably also just a little bit early. It was probably not until a year or so after I'd gone that I think those conversations became really serious in any case.
ZIERLER: Michael, what aspects of your thesis research did you look to expand and refine as a postdoc and, just by virtue of being at Caltech, what new projects did you take on?
NIELSEN: There were really two things that I did at Caltech. One was the book, which we've already talked a little bit about. I worked on it far too hard. That's also where I got very interested in the connection between an area of mathematics—known as majorization—and quantum mechanics and quantum information. It turns that a bunch of mathematicians and economists actually had developed this mathematical theory of majorization much, much earlier for reasons having nothing to do with quantum mechanics. I realized at Caltech that there were pretty deep connections between the way quantum states behave and this theory of majorization. At first, it seemed a little bit like one-off insights. Gradually, as time went on, I realized that there were deep reasons why there should be a lot of different connections. It's difficult to describe without going into a lot of technical detail. But, basically, you have this set of mathematical ideas that are governing the way in which quantum states can be transformed; the way entanglement could be transformed; what determines when a state is separable or not. All these very fundamental questions in quantum information turn out to be connected to this much older area of mathematics, an area of mathematics that comes out of economics, of all places. Exploring that is what I spent much of my time at Caltech doing. It was almost accidentally first realizing there was a connection, and then, as time went on, realizing, oh, no, there's really some very deep reasons why there's a whole lot of different connections.
ZIERLER: Michael, what was the research culture like at Caltech? How would you collaborate, both with postdocs, with graduate students, even with faculty?
NIELSEN: For me, probably the most important thing turned out to be—I gave a series of I think it was six or maybe eight lectures about majorization, just developing the basic ideas and the basic connections to quantum mechanics, which were attended by John Preskill, and by the postdocs who were interested in quantum information, and by the grad students. Some of those students and postdocs got very interested in the subject, and it formed the launching point for a whole lot of conversations and, in some cases, collaboration. Sumit Daftuar and Dave Beckman, in particular, I think, both ended up writing papers about these connections as well, in part as an outcome of work stimulated by those lectures.
ZIERLER: You mentioned Kitaev and Shor. What was your sense of outside scholars, some of the biggest ideas that were feeding into quantum information at that time?
NIELSEN: [laugh] I think I could talk for quite some time about either of those people's work. They've both been very important, I think, for the history of physics and of quantum information over the last 30–35 years. Let me pick one. Kitaev has this very interesting approach, which I think is historically very unusual to doing science. The way in which physicists often work is to study either extant mathematical structures or extant physical systems. You take—I don't know—think about somebody like Onnes, who figures out how to refrigerate very well, and he cools some substances down, and discovers superconductivity. This is a very classic procedure. You just keep extending the bounds of what's possible.
The way I think of some of Kitaev's work was he's really inverting this approach, and instead trying to invent models which have certain specified properties, in particular his notion of natural fault tolerance. It's just an incredible idea, the idea that you can build systems that, in some sense, want to be coherent. They want to quantum compute. This is a complete inversion of the way a physicist would usually think about things. It's very tempting just to focus on the local context, and to say, oh, that's an idea about quantum computing or about quantum error correction. But I think it's a much broader idea. I think it's an idea about what physics is and wants to be as a subject, this idea that instead of just taking the natural next step with extant systems, you could instead start from a design point of view, and say, "What possibilities are latent with the built-in building blocks that we already have?" He's not the only person responsible for this point of view, of course, but I think he's probably the person who's found the most striking examples of it. This is a way in which, I think, physics is really changing.
ZIERLER: Now, I'll ask a more narrow question about Peter Shor. The circumstances of him visiting Caltech, was this because Shor's algorithm, it was immediately obvious the impact this would have on quantum computing?
NIELSEN: [laugh] It depends on who you ask. Gerard Milburn was, I think, at the  meeting where—and this is back when I was an undergraduate—where Peter announced his factoring algorithm. Gerard came back. I said to him, "What happened at the meeting?" He said, "Quantum computing's going to be important now. Peter Shor just discovered this amazing algorithm." This is 1994. I don't think other people were mostly thinking this.
NIELSEN: That's just an example of him being really quite prescient. But certainly the people around me really thought very quickly, oh, this is incredible.
ZIERLER: Michael, of course, this is all in the late 1990s at Caltech. It's a theoretical environment. Was anybody really thinking about experimentation, condensed matter, engineering, what ultimately would put the M in IQIM?
NIELSEN: [laugh] Certainly, at Caltech, there were people: Jeff Kimble and Hideo Mabuchi. But then I only had very limited contact. I'm a theorist who was pretty narrowly focused on theory at that time. It was obviously going to be a very long-term project. Getting one qubit under control was hard enough at the time, never mind doing anything more ambitious. On the other hand, I think Caltech institutionally has been very good at supporting things for very long periods, like LIGO, a classic example, making what turned out to be almost a 50-year commitment. You can do things on that timescale that are just impossible on shorter timescales. Having people like Kimble at Caltech, and a bunch of other people elsewhere, start to take very seriously this idea of engineering matter down to the single quantum level: to an extent I didn't realize at the time it's amazing how much many of those people knew that this was what they were in for; that it was a 20-, 30-, 40-, 50-year commitment, and they did it anyway.
ZIERLER: Perhaps an even more far-reaching question than the engineering behind a quantum computer, was anybody talking about applications at that point, what a quantum computer would be good for if we ever were able to build it?
NIELSEN: There was certainly handwringing a lot about applications. Shor had found this application that was of great national security interest; from my point of view, a terrible motivation for being interested. It's a hard question to answer, and I think part of the reason is I'm not actually that interested in applications of quantum computers. I'm much more interested in the question, what is computation about? What is computation for? I view the applications as a nice consequence of that. But it's not the thing that is fascinating to me. A standard answer then and now is they'll be useful for simulating quantum systems and, indeed, I expect that to be tremendously important. On the other hand, I'm not tremendously excited about that.
ZIERLER: Where I was going with the question was, applications can mean two things: industrial applications but also quantum computing as a tool for physics; those kinds of applications.
NIELSEN: Sure. In some ways, what I would be most excited by, as an application, would be showing that quantum mechanics was wrong or incomplete in some way.
NIELSEN: Maybe if you get your 100 qubits in superposition, you start to notice that they're not quite behaving as they should. For a long time, you're going to think, oh, it's noise in the system. It's imperfections in the experimental apparatus. But maybe if you work hard enough on it for long enough, you end up realizing, oh, no, maybe there's something a little bit broken in the laws of physics. That would be the most exciting. That would be a tremendously exciting application, from my point of view. I don't honestly think it's that likely. On the other hand, I think probably on its own that's enough to justify a very large amount of time and energy spent on this subject. The so-called quantum supremacy experiments of the last few years, I think, are starting to make it less likely that that will be an outcome. The most fun thing of all, if this were to be the case—I don't think it's likely—would be if it turns out that there are deviations from the rules of quantum mechanics, but we can effectively error-correct them away, so you might actually get a deeper theory out of it, and some massive breakthroughs in physics, but we'd still be able to quantum compute, which would be really an amazing speculative outcome. But it's just purely speculation. I don't think it's particularly likely.
Quantum Information in Australia and Perimeter
ZIERLER: You referred earlier to the dismal job prospects in quantum information at this point. Otherwise, were you happy to stay in the United States, or was going back to Australia a pull for you?
NIELSEN: I was a Fulbright Scholar, and one of the consequences of the visa that you accept is that you have to go back to your home country for 18 months, I think it is, or maybe 2 years at the end of your term in the United States. To be honest, I think I probably would've preferred to stay in the United States.
ZIERLER: Tell me about going back as a postdoc to University of Queensland. Were you part of a growth mode that would lead to a large center there in quantum information?
NIELSEN: There was a very rapid growth. I was there initially as a postdoc but then was quickly promoted to associate professor and then professor. That was part of much larger growth mode that was really masterminded by Gerard Milburn and Halina Rubinsztein-Dunlop and David Siddle. We went from having one faculty member—Gerard—to having—I don't know—eight or nine faculty just a few years later, for whom quantum computing or quantum information was their main thing. I think it showed a lot of foresight. [laugh] I complain a lot about institutions, but I can't complain about how they did that.
ZIERLER: Why particularly the University of Queensland? Why did it become the center for quantum information?
NIELSEN: Really, I think, the people who I mentioned, particularly Gerard Milburn and Halina Rubinsztein-Dunlop, the two of them between them just had a lot of foresight. Gerard wrote, I think, the first paper about practical implementation of quantum computing back in 1987 or '88. He knew a long time before almost anybody that this field was going to matter. Halina was a remarkably effective leader within the Australian physics community at gathering support for this, and she understood as well that this was going to be very important over the long-term. It's people: people with courage and foresight.
ZIERLER: To the extent that support of quantum information is in the national interest, did the Australian government specifically support this endeavor at the University of Queensland?
NIELSEN: They did. I might get some of the details wrong here. There was Bob Clark and later Michelle Simmons at the University of New South Wales, who helped organize some kind of national center or national collaboration. I think they got an initial check for—I can't remember—it was like $9 million, or something, Australian, so quite a bit of money, which kicked off a lot of work Australia-wide. Much of that work was experimentally focused. But then Gerard had also been building capacity for some years at the University of Queensland at that point, and so that was a very large part of the overall Australian quantum effort. It's hard to talk about because it's very tempting to want to use these abstractions of a national effort or whatnot. Of course, there's always two competing forces. There's individuals at the bottom, and then there's these top-down forces. There were some decisions taken at the ministerial and possibly even a higher level in Australia. I don't have a lot of vision into those. I don't understand what those decisions were or why they were made. But I'm aware that they were important. I have a lot more vision into the lower level stuff; why individual institutions were making their decisions. I'm just cautioning or really explaining why I don't have a good understanding of what happened.
ZIERLER: Michael, by the time you joined the faculty, what was your key research at that point? What were you working on?
NIELSEN: Two things. One was a set of ideas about optical quantum computing. I mentioned before there was this work on quantum gate teleportation that I'd done seven or eight years earlier. I realized that ideas related to that, and the so-called cluster state model of quantum computation, which Hans Briegel and Robert Raussendorf had pioneered: I just very fortuitously noticed that if you took some common optical elements, and combined them with this very abstract and unusual model of quantum computation, you could dramatically simplify the requirements for doing optical quantum computation. At the time when I first noticed this, to do a single quantum gate using optical elements, on the order of hundreds of millions or billions of optical elements \were required. Then when you've made this combination with this unusual cluster state model of computation, you could simplify that down to on the order of a few hundred optical elements. It's - very, very roughly - a million-fold reduction in complexity.
Then a little bit after I showed that, Terry Rudolph and Dan Brown further simplified my model, basically taking optical quantum computing from being this pie-in-the-sky idea to being something that you could think about really doing in the lab. In fact, Terry has now cofounded a company PsiQuantum, which is aiming to do that, the far descendants of that set of ideas. Anyway, I was working on developing those ideas further and, in particular, showing that they could be made resilient to the effects of noise, and trying to understand just how resilient they would be.
That was one set of ideas that was taking about 50% or so of my time around 2003 through 2007. In parallel with that, I gradually got more and more interested in a reformulation of quantum computing as a type of geometry. This is a strange idea but bear with me as I describe it. The idea is that in the standard approach to quantum computing, you have a bunch of discrete gates which you apply to the quantum state. You try and manipulate it. You try to go through the quantum state space to get to your destination. It's a very discrete almost Lego brick kind of a model. I wondered if there was a much more geometric approach to reformulating it. The idea was to find a very high-dimensional space where I could introduce some notion of curvature in that space. Then the way you think of your quantum computation was simply of moving freely within that curved space, with the local motion determined by the curvature of the space. It's like if you take a sailing ship, and send it off across the ocean, and you just give it an initial push, it will tend to curve around because of the curvature of the Earth's surface. This is a very high-dimensional and somewhat more abstract analog of that. You might say, "Well, why would you consider doing that?" There's a very simple reason, or two very simple reasons. One was if you want to think about optimal quantum circuits for solving problems, in the standard approach, it seems a little bit arbitrary. You add a gate. Then you add another gate. Then you add another gate. There's no notion of gradually making progress towards the optimal outcome. It turns out that in this geometric picture: once you set sail in a particular direction, after that, all of the subsequent behavior is completely determined by the local curvature of space. In particular, using some ideas from the calculus of variations, you get what's called the geodesic equation, which completely determines all the subsequent behavior. That's a radical shift in viewpoint, and so I wondered if there might be some benefit to making this shift, and worked very hard for a few years to try and do this reformulation. I think, certainly, the basic reformulation was quite successful. We were able to show an equivalence of sorts between these two points of view, and we did a lot of work, trying to see what the consequences were. But that was actually about the time at which I moved away from quantum mechanics to doing this work on open science, and I gave the geometric work up with a lot of regret. I thought that set of ideas would likely die. Then six or seven years later, I got this very surprising email out of the blue from Lenny Susskind at Stanford, saying that he was now using this model to study quantum models of black holes, and could I come and visit? [laugh] Apparently, it's now got this second life as an approach to thinking about the computational complexity of black holes. I don't know. Chalk one up for serendipity.
ZIERLER: Do you think this idea will get us closer to a theory of quantum gravity? Is it part of the equation?
NIELSEN: That's way above my pay grade.
NIELSEN: It's lovely seeing people like Lenny or Adam Brown and others excited about that. But I don't know enough to really know whether or not that's right.
ZIERLER: I asked about thinking about experimentation, and actually building a quantum computer at Caltech. What about in Australia at the University of Queensland? Were people at that point, 2005–2006, was this becoming a more realistic proposition?
NIELSEN: Yeah, still very early prototype systems at that point. Andrew White's group, in particular, was doing some work like that. They had some nice papers in Nature, doing very simple optical elements for quantum computing. One of Andrew's postdocs, Jeremy O'Brien, he along with Terry Rudolph is actually the founder of PsiQuantum, the company I mentioned before. They're now super serious and have—I don't know—one or two hundred people, I think, or some large number of people working on it. In that sense, UQ was incubating that effort 15 years ago.
ZIERLER: Tell me about the decision to join Perimeter.
NIELSEN: I left the University of Queensland in 2007 to join the Perimeter Institute. It's a complicated decision to describe. I think the shortest version is just, although there were people in physics at the University of Queensland who were establishing a very good environment, Australia also had a long way to go. One hundred years ago, it was a long way away from the centers of scientific work. Then you have people like Milburn and Rubinsztein-Dunlop who've done a tremendous amount to really bring it up-to-date and, in some ways, to make it a center. But the overall institutional environment I still didn't like. An example was I was shocked—and this will show some naivety— when I became a faculty member at the University of Queensland, and realized that what a lot of people at the university valued was just your ability to raise grant money. This was viewed as a sign of scientific success, and my naïve mind at the time said: "hello, this is crazy". Nobody thinks Albert Einstein was an important scientist because he raised a lot of grant money. It was because he did something for our understanding of the universe. In general, in Australia there is a lot of focus on secondary institutional proxies, which I just found unpleasant. It drives a lot of the way things work. I was shielded from that by good mentors, to a considerable extent, but I still just didn't enjoy it, and so I left to go back to North America, and what I felt or hoped was going to be a better institutional environment.
ZIERLER: Michael, you mentioned previously that while you were still in Australia, you were starting to think about open science. Did you move to Perimeter with the intention that this would be something that you would focus on more, or were you thinking Perimeter is just good for quantum information, and I'm going to go there open-ended in that regard?
NIELSEN: What actually happened at Perimeter, my first day there, the founding director, Howard Burton, it was announced that his contract was not going to be renewed. That was a real shock to me because a large part of the reason I went was because I really admired the way in which he'd set up the institute. He'd been running the institute for, I think, eight or nine years at that point. Arriving and literally walking in on the first day, and there's a meeting of everybody at 9 a.m., and it's said, "Howard Burton is no longer running the institute," caused me to do a lot of reflection about, well, what do I really want to be working on? Certainly, in the few months after that, I thought a lot about, "Do I want to maybe think about shifting my area of focus?" Ultimately, I decided that I did, which wasn't the plan going in. [laugh]
A Major Career Pivot
ZIERLER: There's always a push and pull factor. But to the extent that you thought quantum information was a mature field at this point, did that make it less attractive to you? Obviously, there was low-hanging fruit that remains low-hanging fruit, but perhaps you saw it not exactly in those terms at that point.
NIELSEN: My sense at that point was there's a few hundred people working full-time on theory at this point. There was, depending on how you count, arguably zero people working full-time on open science at that time. It seemed to me like just a tremendously important thing for somebody to be working on, and that certainly played a role. It's also just some question of intellectual taste. I like doing things where I feel a little bit more on my own.
ZIERLER: How did your colleagues take the news when you made this momentous decision? Did they think you were crazy?
NIELSEN: I certainly got some peculiar looks. [laugh] I think a lot were very surprised. Probably a few thought I was crazy. A few thought I was just making a bad decision. Well, probably quite a few thought I was just making a bad decision. I don't think anybody really tried to talk me out of it.
ZIERLER: Where did you set up shop initially when you struck off on your own? Did you come to San Francisco?
NIELSEN: No, I stayed in Waterloo and in the Toronto area for quite a few years. I like Canada, Toronto is a great city, so I was pleased to stick around there. It was challenging not to have a proper intellectual home. I much prefer having colleagues around, even if they're not working on quite the same thing but just adjacent things or there's some sense of sympathy. For some years, I really just didn't have that. I was mostly attempting to work on my own.
ZIERLER: Michael, at the beginning of our talk, you gave some sense of the complexity, the problems that prompted you to work in open science. On that basis, what was the game plan for you? Of all the things to work on, what would you focus on first?
NIELSEN: My initial instinct was to focus on developing tools. I'd been very impressed in the 1990s and early 2000s by things like Linux and Wikipedia. They're really fostering new modes of knowledge production. For a person like me, that focus on tools is very natural. It's a very concrete thing that you can just work on. But as I thought about the problem of open science more, particularly through to 2007, I realized that tools were really a secondary problem. In some sense, the problem of open science is fundamentally a problem of values and of political economy. It's the question of what kinds of scientific work matter in the reputation economy of science? I remember hearing somebody talking about their contributions to MathOverflow, which is an online question and answer site about mathematics, and commenting that they should've been doing "real work" instead of "wasting their time" answering questions on MathOverflow. That's such an interesting value judgment because in terms of intrinsic contribution to human knowledge, it's quite plausible that their contribution to MathOverflow was much more significant. They're making a value judgment based on an internalized set of values about what actually matters to science, but it's not necessarily one which matches the real contribution. Those kinds of questions about values and what people think actually matters are really at the heart of, well, I was going to say open science but, in fact, how we do science in general.
This is very abstract. Let me just go back to Galileo. Some of Galileo's work he "published" in the form of anagrams—I think when he discovered what we would now call the rings of Saturn—he didn't realize they were rings, but he noticed these bumps on the side of Saturn—he sent letters to five of his colleagues, including Kepler, not announcing what he'd seen but, rather, sending them an anagram which, in the event that they later made the same discovery, he would unscramble the anagram to establish his own priority.
From a modern point of view, this is crazy. You would publish the result, and establish your priority in that way. Well, he didn't have such an option, and that's partially a technical deficit, but it's also partially a deficit of values. He didn't see that as part of his role as a scientist. Anyway, to bring it back to your initial question, once I started to see this kind of change in values as being very fundamental, the question became, well, how do you achieve that? One of the things that I thought was most crucial was just trying to get the phrase "open science" into people's heads, and to make it something which they at least had some vague notion of and some opinion of. In particular, I wanted scientists and particularly the people who run scientific institutions to have opinions about that. Once I decided on that, then some kind of advocacy role—writing opeds; writing opinion pieces in places like Nature; writing a book—all those become very natural things to want to do. That's how you start to get people to think about issues like that, and that's how you get that kind of phrase in people's heads. I wasn't the only person trying to popularize that phrase but I think I was certainly one of the earliest.
ZIERLER: Michael, besides living on savings, what was your business model? Did you try to build client relationships? Were you consulting? How did you pay the bills?
NIELSEN: To some extent by running down my savings account. It was, honestly, quite unpleasant, actually, for a number of years, David, and very stressful. I did a [laugh] very small amount of consulting and some things like that but mostly just running out the clock on savings. At the time, I was married, and my wife—now ex-wife—had a small income as well, which obviously helped, but we were by no means doing particularly well financially at that time.
ZIERLER: When you were involved in this full-time, in what ways do you think you moved the needles? What are you most satisfied with in all of the advocacy, all of the writing, all the presentations?
NIELSEN: I think I'm most proud intellectually of having picked a subject at a time when almost nobody else in the world was developing the story of that subject, making it into a coherent story, which other people could pick up and start to think about. It was a transformation in myself in the kind of work I'm able to do, some notion of being able to take a very nascent, very unclear idea, and develop it to a point where other people can start to see and appreciate and have some opinion about, even if it's a negative opinion. But that was a very satisfying arc. It was very satisfying to me when people like Peter Suber and Heather Joseph and Tim Gowers and other people who I admire started to respond to some of my writing. Some of it is just, oh, great, I'm not crazy, but part of it is also this sense of, oh, people whose judgment I respect immensely independently are getting value out of this, and it is apparently beginning to change their thinking. That's just tremendously satisfying for somebody like me.
ZIERLER: As you mention, people can pick up the story based on what you had developed. Where has the field gone in ways that might be surprising to you from your original ideas?
NIELSEN: I'm certainly surprised at the level of government interest in open science. You might've seen recently there was a high-profile announcement: the White House Office of Science and Technology Policy announced that they were instructing all US government departments to develop policies so that if you were funded by those departments to do research, you need to make your papers immediately openly accessible, and you also need to make your data openly accessible. A lot of similar kinds of policy work has been done around the world, so I think a lot of people in government and at grant agencies are very naturally sympathetic to open science, and there's a lot of momentum there. Obviously, I've only played a tiny little role in that, but just having a tiny little role in that is extremely satisfying.
ZIERLER: I wonder if you've thought in broad historical perspective about the move toward open science as, you know, was science ever open in a previous era, and you're looking to return to that, or is this truly new in the 21st century, what you're trying to accomplish?
NIELSEN: The point I took from Paul David's work, in particular, was that there really was a first open science revolution back in the 17th century. It's a constructed state of affairs that moved us from Galileo sending anagrams around to his buddies, to people in the 18th and 19th century openly publishing stuff. That's not a natural state of affairs at all. It had to be achieved by a whole lot of people who realized the value in open disclosure of knowledge. It just happens that at the time, the best thing we had available was the printing press, which is quite slow. It takes many months to go from a manuscript submitted to being published and widely distributed, but that was the best approach to open science which could be managed at the time, let's say, the late 1600s through 1700s. The situation didn't really change that much technologically over the ensuing couple of centuries. It just happens that around 1990 or so, we get this big upgrade in technology, but it's fundamentally the same type of shift which is going on. It's just the technological capabilities are a little bit different today, so it makes sense to do something like—a good example would be something like the Human Genome Project, where they adopted a set of principles in the mid-90s, the so-called Bermuda Principles, which meant that as soon as the genome data was taken—I think it was any read of like 1,024 base pairs or some very short sequence length—they would be publicly shared within I think it was 24 hours. That's a natural extension of what somebody like Henry Oldenburg would've wanted in the 1600s. It's just Henry Oldenburg didn't have the technological ability to enable that kind of sharing. So it's a modern repetition of that earlier shift, but with a very different set of tools and capabilities; it's the same fundamental shift which is going on.
ZIERLER: The Human Genome Project, of course, is in international collaboration. I wonder to what extent national boundaries place a block on open science; that it can't be truly open while we have different governments with their different mandates.
NIELSEN: One of the most common objections that you hear to something like, for example, the open-access mandates, is people will say, "Well, yeah, I get it, the American taxpayer has paid for this research. Americans should be able to read it, but why should we be making it open access to other countries who we might not have a friendly relationship with?" It's an interesting argument. I think, ultimately, it doesn't have much force. The returns to, say, the United States on just doing that basic sharing are so high that any negative impact is very, very small by comparison. Basically, you really want the positive impact of being able to do that kind of sharing. You would need to make a case for an extremely large negative impact, which we just don't seem to see, before it becomes a credible obstacle. But it is an argument that people will sometimes make.
ZIERLER: In 2015, when you went to New York to become a research fellow at the Recurse Center, was that so that you could continue in this work but have an institutional affiliation, or was there a separate intellectual interest there?
NIELSEN: To be perfectly honest, what happened there was that was the time at which I got divorced. That's the honest answer: I needed a change. I knew and liked the people at the Recurse Center. They said, "Why don't you come to New York for a year, and work on the things that you find interesting?" I thought, "Great. This is exactly what I need," so I did. They were terrific.
ZIERLER: Tell me about the Recurse Center. What is its mission, and how does it connect to open science?
NIELSEN: By that point I'd pulled back on the advocacy work on open science, realizing that I am not the kind of person who is an effective advocate. I don't like doing the kind of coalition building which is required. I'd shifted my interest to something parallel, directly working in the tools which people use to do creative work, that is, the tools which would be enabled by open science. I more directly focused on that tool building because I didn't want to continue doing the advocacy work. It was just not a good personality match. Organizationally, the way the Recurse Center describes themselves often is as a writers' retreat for programmers, or sometimes it's almost like a little artists colony for programmers. Suppose you take seriously the idea that programming is a very creative vocation where people can make these beautiful gems. A lot of programmers, they're a little bit caught. They love programming. They love making things inside the computer. But then, often, to pay the bills, they're doing what they feel is much more prosaic things. The Recurse Center has created a space where such people could take a three-month break from their career, and go and work on just making the beautiful things that they want with code. In practice, some of the people are very new to programming. They're just getting into it. But they've also had some very famous programmers go through and participate. It's a very nice environment, full of very idealistic people who are often growing in unusual ways. It was a very pleasant place to be for a year.
ZIERLER: Was it productive? Did you get good work done while you were in New York?
NIELSEN: It was the reset I needed at the time. As I say, I was shifting from doing this kind of advocacy work around open science to doing more direct tool-building work in the same vein, and that tool-building was something I was very new to. Usually, I find it takes about three years to come up to speed in a new area, and the Recurse Center was really the first year of that for me. In retrospect, it's always very frustrating at the time: it's like: "this is very slow; I'm terrible at this". But after a year or so, I wasn't so bad at it. I can see that I really changed a lot in my ability to do that kind of work.
Recurse Center and the Future of Open Science
ZIERLER: What prompted the move to San Francisco?
NIELSEN: The Recurse Center was always likely to be temporary. I wanted a year, and then this opportunity opened up in San Francisco. It's a similar opportunity in many regards. Y Combinator, which is often described as a seed-stage venture capitalist, was starting a not-for-profit research arm, which was going to be focused on very basic, very fundamental, very open-ended research. I'd been chatting with the head of Y Combinator, Sam Altman, at the time, just about research in general, and I decided to come out and be part of that. It was a continuation in terms of the work; very much a continuation. The research direction didn't change at all but there were just more people and more stability, partially internal to the organization, but partially also because the Bay Area is just very open to that kind of work.
ZIERLER: Michael, I wonder, just being a research fellow, being a paid employee, how did that affect your bandwidth to just focus on the things that were most important to you without worrying about making a business out of it?
NIELSEN: It's tremendous, it helps so much not having to worry. Academia is often described from the outside as this idyllic environment in which people get to think their thoughts. For me, at least, environments like the Recurse Center and YC Research and Astera have approached much more that ideal of providing an intellectually stimulating environment where I have a tremendous amount of freedom to pursue the work that I think is most important.
ZIERLER: Have you kept up in neural networks since 2015? Is that something that's been a central interest for you?
NIELSEN: No, it's never been a central interest, but it has always been this side hobby interest, something to do if work is a little bit slow or I need a break for a day or two. It's one of the most exciting things that's going on in science at the moment, and so I follow a bit. There's a lot of people who are working on this, of course, so you bump into them, and get to chat, and hear what they're doing. It's very exciting.
ZIERLER: Michael, I'm curious, the social isolation mandated by the pandemic, the dark days of 2020, I wonder to what extent that influenced your ideas about the production of knowledge, and how science is done.
NIELSEN: I've talked a lot, as I think everybody has, to friends and colleagues about what it's meant for people's lives and for their work. One of the striking things for me is that no really coherent picture has emerged. I've talked to people who say, "Wow, I got so much more done." I've talked to other people who tell me, "Oh, it was terrible. I couldn't get anything done." Other people say, "I got a lot done but then I find my ideas drying up." It's difficult to say. I'm not sure I have a strong sense of what it's meant. Obviously, there's this well-documented shift to remote work, but the way in which the remote work has instantiated is still changing very rapidly. I don't think you should expect that to be something which institutions sort out over six months or even two years. It's more like something which is going to take 10–20 years, to actually sort out how to do it well.
ZIERLER: In 2019, when you started thinking about the essays that would lead to Quantum Computing for the Very Curious—
NIELSEN: Oh, yeah. [laugh]
ZIERLER: —was that a way for you to dip a toe back into the field? Was that purely fun? What were your motivations?
NIELSEN: It looks like an exercise in quantum mechanics but it had nothing to do with it. I was working with Andy Matuschak on tools to change the way people think and create, and we needed a subject to use as the environment in which to operate. I was like, "I can write about quantum computing. I barely need to think about it [laugh] at all." It was just a very convenient, very handy prop to use. In fact, almost all of the creative work in that project had nothing to do with quantum computing. A tremendous amount of thought went into that project but none of it was on the quantum computing side. [laugh] It was almost automatic writing.
ZIERLER: Michael, we've already covered what you're doing currently, so for the last part of our talk, I'd like to ask a retrospective question, and then we'll end looking to the future. Between quantum information and open science, I wonder if you've thought broadly about the Kuhnian idea of scientific revolutions. Both quantum information and open science were not areas that he thought about. But to the extent that you believe in that paradigm—and I don't know if you; that's a question in and of itself—how does your expertise or the reality of these fields influence the idea of scientific progress, the idea of scientific revolutions?
NIELSEN: Just focusing on Kuhn, he had a very narrow sense of what a scientific revolution is. One of the most common criticisms of him is that he was too focused on physics in particular; and to some extent, chemistry. He was originally trained as a theoretical physicist, and it really shows in his writing. Something like quantum mechanics or general relativity is disrupting an existing order. Well, quantum information isn't disrupting any existing order. It's not like there's a whole bunch of ex-classical information theorists who are, all of a sudden, put out of a job because they've been superseded by this new notion. In that sense, just a whole lot of his description doesn't apply. It's too narrow a way of thinking. Still, I loved his book. I read it when I was, I think, 18 or 19. It's deeply influenced the way I think about science. But I also think it's wrong in a whole bunch of important ways, and too narrow. It's not a good description of either quantum information or of open science. Open science is, as I said before, really a revolution in the political economy of science. That's what it is most fundamentally. He barely talks about political economy at all in that book.
ZIERLER: Michael, two last forward-looking questions. Where is open science headed? What are the frontiers in this area, and where do you want to contribute?
NIELSEN: My personal contribution continues to be what it's been since about 2013 or so, which is just engaging in the practices. That's what I'm happiest doing in my own work, so sharing work as widely and as early as possible, building tools, and working in the open as much as possible. In terms of the broad question, there's a tremendous amount of momentum at the institutional level, governmental level, the grant agency level. I'm happy about that mostly. I wish there was a more functional market for media tools, including journals. That lack is a real problem. That's maybe a longer thought than we have time for. Running things through centralized mandates is a pretty poor way to—that's the thing that you do when you don't have a better option. You can end up in a situation where it's mandated that everybody share data on such-and-such a platform, and that is a recipe for lock-in over the long term. You use your whiz-bang platform to share data and, 30 years later, you're still using that platform which, by that point, is way, way, way out of date, and there should be much better options. That's something I worry about, and it's something that I worry is not being addressed sufficiently well: basically, having some kind of effective marketplace which is dynamic and which enables continual updates in the tools which people are using, and which people are enthusiastic about. That's a concern. I don't know what to do about it. I talk about it with people occasionally. We'll see.
ZIERLER: Finally, Michael, a fun question, one to prompt you to see if you'll say never say never. Is there a development or even a revolution, if you will, in quantum information that might pull you back into the field, and, even if you wanted to, is there a concern that a certain amount of muscle memory is lost where that might not be feasible?
NIELSEN: To the second question, yeah, I'm way out of date. I'd have to go back and start as a PhD student, in many regards, again. I can't see what would make me go back. In making career decisions, you want to move towards things where you have a unique ability to contribute, and I just don't see that there's any possibility of that there. I would rather work on things where I see some unique ability to contribute or, at least, ability to develop such an ability, so to speak.
ZIERLER: But that's more a reflection on you, and not about the field, necessarily?
NIELSEN: Absolutely. You make your choices. Long ago, I made the choice not to become a 100-meter runner—
NIELSEN: —and that has only looked like a better and better choice over the years since.
NIELSEN: The difference is not that large. Obviously, I was probably considerably better suited to work on quantum information than I ever was to run the 100 meters. But there's a window and, at some point, you step out of that window. But the environment can change. I guess that's where your question is pointing at. The environment can change, and it is possible, I guess, at some point in the future that the environment would change in such a way, I would look and I would say, "Oh, wow, there's an opportunity for me to contribute in a way that is really valuable and significant." I just can't imagine what that is at the moment. But if it happened—
ZIERLER: We'll see.
NIELSEN: —I'd consider it. It'd be fun.
ZIERLER: Michael, this has been a phenomenal conversation. I want to thank you so much for spending this time with me.
NIELSEN: Thanks so much, David.
- Surprises in Quantum Computation
- Connecting Quantum Information and Open Science
- Open Science and Public Communication
- From Australia to New Mexico
- Caltech Before the IQI
- Quantum Information in Australia and Perimeter
- A Major Career Pivot
- Recurse Center and the Future of Open Science