Narratives and the justification of science
Dave Bacon asks why his field doesn’t get enough lovin’ among other scientists:
The number one most irritating question I was asked during my faculty interviews was “what will you do if quantum computation doesn’t pan out?” […] And this is what makes the question so irritating: it implies that quantum information science is a fad with no intrinsic intellectual value. Do you ask string theorists whether what they do will be experimentally testable and if not what will they do? Do you ask astrophysicists whether studying cosmology will have any significant impact on society? No. But because these are part of a long tradition of theoretical physics they are acceptable intellectual persuits, whereas quantum information science, being new and getting too much press is most definitely suspect.
I suspect that in the last sentence Dave has put his finger on part, but only a small part, of the problem. I think there’s an another consideration that plays a much bigger role.
String theory, astrophysics, and (to a lesser extent) condensed matter and AMO physics have all done a terrific job of articulating why they matter. They’ve identified deep central questions that are relatively timeless and unarguably important. Furthermore, they’ve communicated those questions clearly and repeatedly, not just within physics, but to other scientists, and, in some instances, to the public at large. Even if the specific approaches they are taking to those questions fail to work – maybe string theory won’t pan out, or gravitational waves won’t be detected, or whatever – the questions will remain important.
Contrast this with quantum information science. Most presentations on quantum information science I’ve seen motivates the field either by saying (a) quantum computing has important practical applications, and so should be pursured, or (b) by making vague allusions to the importance of better understanding quantum mechanics.
In short, the quantum information science community hasn’t fully articulated a sensible narrative containing questions that are big, timeless, and important. And until such a narrative has been articulated, and communicated to the world at large through review articles, overviews, technical and popular books, other scientists will wonder legitimately about the value of the field.
This problem isn’t unique to quantum information science, of course. I’m just using it as an example because Dave used it, and I happen to feel strongly about it. The problem affects many other fields; a good example is complex systems research, which I’m pretty sure has suffered some of the same problems, though in somewhat different ways.
I’m personally convinced that there are big and timeless questions that can be addressed by the techniques of quantum information science. I’ve tried to describe some of these questions here and here and here. (The first article is in Scientific American, and I’m not sure it’s accessible without an institutional subscription.)
This really needs a lengthy post, but in brief I think a big and important problem that can be addressed by quantum information science is to understand the behaviour of complex quantum systems. That is, we want to find general principles governing complex quantum systems, and determine what makes them different from complex classical systems.
This problem is not unrelated to some of the central problems of condensed matter physics, but I think there’s a key difference in approach. Quantum information science starts by taking quantum mechanics very seriously – some would say too seriously – and asking what is possible within the confines of that theory. Condensed matter physics has been much more motivated by experiment, and by the pursuit of some key theoretical models. I think that’s a great thing – condensed matter physics has had fabulous successes beyond number – but I do think the different perspective of quantum information science has something important to contribute.