## The next big thing?

July 10, 2011

Quantum information theory has evolved in fascinating ways over the past two decades or so and I’ve been privileged to directly witness its development for ten of these years. In this post, I thought I’d have a go at predicting where it will go, and what the “next big thing” for quantum information theory will be.

Around the year 2000 quantum information theory seemed to be primarily focussed on two broad themes: building a quantum computer and developing quantum algorithms for it, and building a resource theory for quantum information via, e.g., quantum entanglement theory and quantum Shannon theory. To a large extent both of these themes continue strongly today. Although, I’d suggest that quantum Shannon theory has fared much better than the theory of quantum entanglement, in particular, that of entanglement measures, which seemed really important a decade ago but not so much now.

One thing that would have been harder to predict was the influence of quantum information theory on other areas of physics. For example, QI has now had some considerable impact in condensed matter physics, particularly with regard to the development of new classical simulation algorithms for complex quantum systems. From my considerably biased perspective I think that this second-order effect has been rather important. Also, there has been excitement about the role and influence of QI on biological physics.

So now to the question: what next for quantum information? I based the following list on topics that I personally find very interesting, and also on observations I’ve made about external pressures coming from funding agencies and from the job market.

1. Quantum computers

I firmly believe a quantum computer will be built, although I refuse to say how long this will take. One thing that I think may happen is the emphasis on fault tolerance thresholds in choosing a quantum computer architecture will diminish slightly as experimentalists engineer systems capable of supporting quantum coherence on longer timescales. I’m sure that cluster states will be exploited in some way in the successful quantum computer architectures. I also feel sure that as we get access to such systems this will spark our creativity in designing nontrivial things to do, i.e., in developing quantum algorithms using dissipative quantum processes.

2. Quantum algorithms

Thus I feel convinced that quantum algorithms development will continue, albeit slowly. One area which hasn’t received much attention — probably because it isn’t as glamourous as an exponential speedup — but which really should, is the development of quantum algorithms which give polynomial speedups for problems in P. These kind of speedups could turn out to be extremely important: if the best classical algorithm for a problem of major practical importance uses, say, ${O(n^3)}$ operations, and you found a quantum algorithm using ${O(n\log(n))}$ operations this would have major practical implications. I do hope that such speedups will become an area of more intense research and I feel relatively confident this area could take off. Unfortunately I don’t know enough about classical algorithms to give a firm prediction for which kinds of problems will be amenable to such quantum speedups (sorry!).

As mentioned above, another class of quantum algorithms which has been so far relatively unexplored, is that of dissipative quantum algorithms. (There are some exceptions here, see, e.g., and this, this, and, somewhat immodestly, this.) Such algorithms are extremely important because they give intermediate experimental implementations something to run!

3. Complex quantum systems

Quantum information will continue to play a role in the study of complex quantum systems. This is an easy prediction: QI trained people are generally quite good at thinking about quantum coherence, which plays a major role in the physics of strongly interacting quantum systems. I feel relatively confident in predicting that the physics of 2D and, to some extent, 3D lattice systems, will see major QI-inspired developments.

Another area which I am very enthusiastic about is that of quantum systems with continuous degrees of freedom, particularly, quantum fields. Lattice systems are, after all, an approximation to these systems, and it is clear that existing QI-inspired techniques will have some influence here (indeed, this is just beginning with the extension of MPS and MERA to the continuous setting). Additionally, if a good enough interplay can be developed then this would allow quantum field theorists to be able contribute to quantum information-type problems. Also, holographic correspondences such as the AdS/CFT correspondence have QI aspects, so we might see QI theorists and string theorists working together more strongly here.

4. Classical physics

My final prediction concerns the influence of QI on classical physics. The thing is, QI trained people are not only good at thinking about quantum coherence, but also about correlations in general (see, e.g., the continuing developments in the study of Bell’s inequalities, cryptography based on no-signalling, etc.). Correlations are always hard to think about, but the thing we’ve learnt in studying QI in the context of condensed matter is that if you have a way to think about correlations in a better way then this can lead to new simulation algorithms. Here I have in mind, for example, the study of fluid dynamics, as applied to the climate (see this for a longer discussion), and other problems of classical many body physics such as traffic flow via this, community detection, and image recognition. The nice thing about these areas is that they are much more directly connected with our everyday life. Any contribution here would have a much more direct impact on important problems facing humanity.

What do you think?

## Speculative idea: the genus of an eigenfunction and Kac’s “can one hear the shape of a drum?”

February 22, 2009

This post will be of a different nature to my other posts: I want to talk about a speculative idea that: (i) I had while sitting in a talk; (ii) I haven’t worked through at all; (iii) involves higher power mathematics than what I have at my disposal right now; and (iv) may be stupid, wrong, too naive, or already well-known.

These kind of ideas occur to theorists all the time and, due to resource constraints (i.e., time, energy, money, etc.), seldom get mentioned, except to, say, a conference speaker, and are quickly forgotten by both parties by the time the conference is over.

However, with access to this new medium I hope to broadcast these ideas to more people, some of whom may be experts on the maths required, and maybe, just maybe, someone will be inspired to check it out.

Dumb questions are especially encouraged in these posts because, after all, I’m posting about a dumb question!