Theorists collaborating with experimentalists: a tentative guide

This post is triggered by some of my students. I could give them my own advice directly, but I prefer to write it here because they may benefit from other valuable feedback. The issue at stake is pretty specific: the role of theorists collaborating with experimentalists. The background is my own, limited experience, the classification is as crude as it gets, the analysis proposed here is not the only possible one and is not even always suitable — so, let’s start!

It seems to me that theorist can contribute in four ways to experiments:

  1. Vision: come up with a new concept. It can be very general (say, quantum optics; quantum computing; quantum cryptography) or more specific (say, squeezed states; measurement-based quantum computing; quantum repeaters), but in any case it opens paths that were unexpected before. You won’t find these ideas planned in research proposals: they “happen”. I don’t suggest you base your career on the hope of having such a flash of genius (though you should be ready to recognize it, if it comes).
  2. Tools: develop the necessary theoretical understanding. To continue with the examples above: develop the formalism of quantum optics; invent fault-tolerant architectures; provide the formalism to do security proofs.
  3. Proposals: suggest that a given experimental setup can be used to observe some interesting effect, and do a rough first feasibility study.
  4. Specific description: take a real experiment and describe the physics, to the point where your theory matches the data.

As you can understand, these categories are not tight: for instance, some proposals make it directly into an experiment (nowadays, this is the route of choice to publish your proposal in Nature).

OK, now: here you come and have to decide in which direction to go. You may want absolutely to study a type of experiment: then you need to know what people in that field would appreciate. Or you may want to spend your life (say) inventing proposals: then you need to assess which experimental field is ripe for those. In both cases, the crucial insight for me is: there is a strong correlation between the role of a theorist and the stage of development of the experimental field:

  • At the beginning of a field, proposals are really important; they are also the fast way to celebrity (example: Cirac-Zoller first proposal of a logic gate in quantum computing). If you are up for a longer-term investment, go for tools even at this stage: your effort will be appreciated with a lag, but when the moment comes, you are seen as a pioneer and you are among the few of can really make a difference (example: the work of Norbert Lutkenhaus on unconditional security of quantum cryptography).
  • Once the field is mature, proposals must become really relevant (some physics journals can be seen as a cemetery of irrelevant proposals). Rule of thumb: if no experimentalist cares about your proposals, with overwhelming probability you are not the misunderstood genius, but just the delayed fellow (though, of course, exceptions are possible). At this stage, tools are the most appreciated contribution of theorists: if you develop them, you can choose to keep contact with the labs, or you can take the way of mathematical physics and develop them for their own sake. Both ways are serious; my advice is, but whichever you take, keep an eye on the other.
  • When a field is so mature that even the tools are fully developed, there is little left to do other than specific descriptions (this is the case, for instance, of quantum optics per se, i.e. aside from possible applications in quantum information). Specific descriptions of experiments are tricky. First, you need to check if the experimental group “needs your service”: some groups, for instance, have developed their tools so well, that their experiments are “textbook experiments”, which means that anyone who can follow a textbook can do the theory. Now, if your help is welcome, it is normally very welcome. Since there few people able to do that (compared to the mass of people contributing to the cemetery of proposals), you will be noticed among the experimentalists and may be asked for various collaborations. This is great for a PhD and, if you have such competence, you would do well in keeping it alive for the rest of your career. But you have to do something else as well, if you want to get a position: you need to show that you are also capable of original work (see why in a previous post).

About valerio

Principal investigator at Centre for Quantum Technologies and professor at National University of Singapore

Posted on March 14, 2012, in Career, Quantum. Bookmark the permalink. Leave a comment.

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