In Vienna, Virginia on April 23-25th a workshop is being held in response to a report, “A Federal Vision for Quantum Information Science” issued by the United States National Science and Technology Council. While this workshop looks, from the outside, like any other typical quantum computing workshop, this is a bit deceiving, as from what I understand this workshop is supposed to provide the impetus for a report arguing for a major spending for quantum information science in the United States, especially from the National Science Foundation. The Quantum Pontiff, unfortunately, is stuck unquantumly pontificating before his intro to computer science theory students, so he won’t be able to attend the workshop. Which is all to say this is as good of place as any to write down my own thoughts on what a national initiative in quantum computing should look like. (Of course my qualifications to make such a judgment are thin at best, being a second-rate pseudo professor from the nether regions of quantum computing. But ain’t blogs great. On the internet no one knows you’re a research assistant professor!)
My own bias as to what any national initiative should be is already quite evident in the last paragraph, and well…it’s blasted into the title of this post. I said a national initiative in quantum computing, not a national initiative in quantum information science!
Let’s begin where the impetus for the workshop starts: with the report on a federal vision for quantum information science. First of all let me say how nice it is to read a document that says “federal” on its title page but that presents a very nice description of quantum information science. The authors should be commended for somehow avoiding the federal bureaucracy fudging-it-up filter (maybe it was even more technical and precise before going through this filter?! And by the way, who wrote the document, there are no names of the mysterious subcommittee which produced the document.)
The summary of the report is provided by the document itself:
The scope of the scientific challenge that must be addressed if we are to fully exploit the potential possibilities that QIS provides for 21st century technology is encompassed in the following three fundamental questions.
- What is the true power of a general purpose quantum computer, what problems does it allow us to compute efficiently, and what does it teach us about nature?
- Are there fundamental limits to our ability to control and manipulate quantum systems, and what constraints do they place on technology and QIS?
- Are there exotic new states of matter that emerge from collective quantum systems, what are they useful for, how robust are they to environmental interactions, and do these collective quantum phenomenon limit the complexity of the quantum computing devices we can build?
This is a great summary of three major intellectual challenges arising from quantum information science. They are the questions that get you up out of bed in the morning wondering what new and interesting facts you will discover about how the world works. These are the bread and butter of current academic research into quantum information science, both in theory and experiment, and deserve to be funded at a high level.
But let’s take a step back for a second and consider not what is included in that document, but what is missing. Do a search for the world “build” in the document. Do a search for the word “quantum computer” and look at the surrounding sentences. Notice something funny? Missing from the document is any actual mention of the desire to actually build a quantum computer!
Now, I’m going to be the first to say that support of fundamental research into the broad field known as quantum information science should be supported. I will argue to my deathbed that it’s exactly the kind of fundamental research that could pan out big, not necessarily today, but in the future, reveals much about our universe, and challenges our current understanding of fundamental limits of computing in the universe. It’s exactly the kind of research that the NSF should fund at a level higher than that they do today (but thankyouverymuch NSF for your support of my research ), and that agencies such as IARPA, DARPA, ARO, and the NSA have been funding very strongly since Shor’s discovery of a quantum algorithm for factoring in 1994. But, as Dorit Aharonov so wisely said to me while at QIP last year (paraphrasing) “Quantum computing isn’t interesting without a quantum computer!” Which isn’t to say that the kind of research described in the report shouldn’t be funded: indeed Dorit herself is a fine example of what you’ll get for such funding, a bunch of awesome results challenging what we understand about information processing in the quantum world. And for researchers in quantum information science, there is value in their research, because there is the prospect that it will be much more than just exercises in their head, but that someday their ideas will find their way to actual hardware exploiting quantum effects. But, really, at some point you have to stop and ask yourself (as happened to me when Dorit chewed me out ) where is the major push to build a quantum computer?
There is a tendency in quantum computing to not want to promise a quantum computer. Despite what you might read in EurekaAlerts! or New Scientist, most quantum computing researchers are very conscientious of trying to avoid hype (resistance to hype being strongly correlated with distance from tenure decisions.) And, this caution, for a long while, has been very much justified. In the year 2000, for example, there were not many physical implementations of quantum computers that had passed the proof of principle barrier (ion traps being the only one in the ballpark.) But results since that time have been tremendous. Which brings us to the question, is it still true that quantum computers are “a decade away?” And, even if quantum computers are still a far off, is this being aided or abetted by the current way in which quantum computing is funded?
Recently, in thinking about what I wanted to do with my life, I sat down and did some deeper reading into the experimental progress in quantum computing over the last few years. When I graduated from Berkeley in 2001, I made a very conscious decision to focus my own research very much on the computer science side of quantum computing. I tried to work on quantum algorithms because I thought not enough people were working on quantum algorithms (and if I could make any small progress then maybe people much smarter than me, that is to say everyone, would say, “hey if Dave Bacon can work on quantum algorithms than so can I!”) I worked on ideas for self-correction because I was deeply skeptical of approaches to build a quantum computer which don’t take error correction as a fundamental objective of a physical implementation. To this day if there is one thing I could say to every experimentalist working in quantum computing it would be “deeply absorb how quantum error correction works!” And I most specifically did not focus on work that was closely tied to one particular physical implementation of quantum computers. This later fact was, in large part, because there were not any implementations I could latch onto as having the potential to be the one which would scale, in the coming decade, into a large usable quantum computer. But in reviewing the progress over the last five years or so, I don’t believe I can as easily conclude this.
Now I’m but a mere theorist, probably only experimentally capable of reproducing Feynman’s sprinkler a la a Feynman explosion, so my judgment about the viability of different potential implementations of quantum computing is probably highly suspect. But from my perspective, both ion traps and, increasingly, superconducting qubits seem to me to be close to the stage in which the questions are increasingly not the kind which focus on one or two qubit devices, but are at the stage, or will be at the stage in a few short years, where the issues will be how to construct quantum computers with hundreds to thousands of qubits. I would also say that one benefit of hanging out in a Computer Science and Engineering department, is that one begins to actually appreciate the power and difficulty of engineering and how the ultimate challenge to building a quantum computer will come explicitly from these challenges. Of course all of this is for naught if the basic one and two qubit gates and technologies for building larger numbers of qubits is not in place. Ion traps are certainly well within the regime where one can consider fault-tolerant quantum computing, the main challenge being the creation of viable scaling technologies for traps, a topic which has met with recent great success (see Wineland group’s heating rates and going around corner traps.) Superconducting qubits of various forms have now implemented the basic gates, achieved impressive single qubit gates, and shown amazing progress with methods for coupling these qubits to microwave cavities.
All of this, to me, then, begs the question: is it time for a large scale push to take one or two of these implementations are attempt to scale them up? Which brings me to the title of my blog post: a big science project to build a quantum computer.
Inevitably when one thinks of projects like this, the word which immediately comes up is “The Manhattan Project” (this connection is drilled into the brain of every physics graduate student: the bomb equals funding for physics.) But, actually, there are tons of other examples from which to draw concerning projects which are engineering tour de forces, in which a community of scientists and engineers has taken the initiative to undertake a task on scale of a major attempt to build a large quantum computer. I think, of course, of large chunks of the space program, the Apollo project, the Voyager missions, etc, and also of numerous large telescopes built over the years, space based missions for astronomy, and the LIGO project. Then of course there are high energy projects like the current multi-billion dollar large hadron collider and the ITER fusion project. Each of these projects is deserving in it’s own right: many challenge our sense of exploration, our quest for fundamental knowledge, and even the future of energy consumption on our planet. And, because I am fully converted, I will argue voraciously that the building of a large quantum computer can compete with any of these projects in terms of public good.
To quote from a policy piece I co-authored with Scott Aaronson:
…quantum computers will…revolutionize large parts of science… Simulating large quantum systems, something a quantum computer can easily do, is not practically possible on a traditional computer. From detailed simulations of biological molecules which will advance the health sciences, to aiding research into novel materials for harvesting electricity from light, a quantum computer will likely be an essential tool for future progress in chemistry, physics, and engineering.
Now I’m enough of a theorist to always worry about the promise of algorithms on quantum computers, but not enough of a skeptic to not think that the original insight into why we should build a quantum computer: that it can be used to simulate quantum systems (and by simulate I do not mean “measure the energy levels” hrmph) in regimes where our modern computers will not succeed. Just the other day, for example, I was learning about how certain microscopy/spectroscopy is limited by the simulation computer power needed to make sense of the data extracted from quantum simulations of these systems. I strongly believe that a quantum computer will be an essential tool for understanding large chunks of chemistry, biology, and material science.
Thus I believe that (1) the justification is there, and (2) increasingly the science is there. I also believe that a large initiative will be needed. This is mostly because of the requirements for fabrication and engineering needed to overcome the challenges faced in building a large scale quantum computer are, I believe, not the kind of challenges which are best suited for a typical academic setting. Say what you will about D-wave, for example (well, as the only example!), but at least they realize that the kind of fab and engineering needed to attempt building something like a quantum computer is not the kind you’ll find within the realms of most of academia.
Now in the large sense the idea of a national initiative to build a quantum computer is fighting against history. Historically, quantum computing has been a romper room for theorists, and a place where physicists could push the limits of quantum control and our understanding of the physics of quantum coherent systems. There is an inertia here caused by a spreading of money to many different groups attempting many different physical implementations of quantum computers. But what happens when the road to build a large quantum computer becomes more apparent? I believe the path forward should be to take the implementations that show this promise and drive forward. I believe that build a quantum computer is a machine we should be shooting for, not some happenstance which helps me get funding. This is not to say that I do not support fundamental research in quantum information science: I think exactly the opposite. But I’m for my cake and eating it too: adding a major initiative to actually build a quantum computer to NSF funded support of the broad area of quantum information science.
Of course my opinion on this whole thing is worth snot if it isn’t at least shared by other scientists and engineers, by the funding agencies, and by the politicians who would be at the heart of funding such a large initiative. In dark alleys at quantum information science meetings I sometimes meet those who really truly desire to build a quantum computer. We give a secret handshake, pay attention to the talks with the most promising technologies, and debate what the word “scalable” actually means. I for one, however, am coming out of the dark: I believe it is time to think of shooting for the stars and build a a large quantum computer.
There. Hopefully that will at least provide some minor fodder for the workshop. Who knows, maybe even a few other members of the secret order of “those who want to build a quantum computer” will be drawn out into the light.