Sunday, August 15, 2010

A turbulent claim?

On Friday we had a nice clear and stimulating physics colloquium, Turbulent times in quantum physics from Brian Anderson.

What are unique characteristics of turbulence?
A beautiful video of a dragon fly in fluid flow was shown to illustrate this.
1. continuous flow
2. unpredictable flow details
3. eddy formation, interaction
4. rapid mixing
5. energy input at one length scale and energy dissipation at another length scale.

The latter is described in a landmark paper from 1941 by Kolmorgorov. He used dimensional analysis to show that the kinetic energy spectrum
E(k) ~ k^-5/3 where k is the wave vector.

A superfluid has no viscosity. But turbulence is still possible. Feynman suggested in 1955 that this could arise as a disordered tangle of vortices.

Three features of quantum turbulence
1. dynamics is described by a quantum dynamical equation (e.g., a non-linear Schrodinger equation) rather than the Navier-Stokes equation.
2. Kolmogorov scaling (this was observed in 1998)
3. disordered tangled arrangement of vortices

BECs have "high potential" for step-by-step construction of a quantum turbulent state.

There are only a million atoms in the BECs studied here.
[But isnt this just 100^3? What is the max. no of vortices one could put in such a small system, 100?]

Spontaneous vortices can be produced with a temperature quench.
It was claimed that dissociation of vortex-antivortex pairs is related to quantum turbulence. However, in two dimensions this dissociation is just the Kosterlitz-Thouless transition which I doubt this has anything to do with quantum turbulence.

Quantum vs. classical turbulence in two dimensions was discussed.
Jupiter's great red spot is considered to be an example of the latter.
Two dimensions leads to different kinetic energy scaling for quantum turbulence, E(k) ~ k^ -3 for large k
Numerical simulations claim to see a crossover to this scaling [However, the graph shown did not appear to have a horizontal scale and so one could not see how may decades of k this covered].

The take home point of the talk was meant to be:
Atomic quantum fluids are enabling advances in difficult physics problems that are relevant beyond quantum physics labs.
However, I failed to see these advances from the talk. The experiments are beautiful and fascinating. But, I could not see how the experiments or simulations have led to any new insights or advances beyond those from Kolmogorov in 1941 and Feynman in 1955. To me this is another example of how people in the BEC community oversell the significance of their work. Potential advances and hoped for insights are not the same as real advances and insights.

For an example of a real advance in a difficult problem which spread across disciplines consider the case of the Hopfield net, which was influenced by ideas from spin glasses in condensed matter physics. This had a large influence on neural networks in computer science and biology. The fact that Hopfield is now a Professor of Molecular Biology at Princeton is a testimony to the advances he made.

Chemical Engineering departments now regularly hire faculty who do research using density functional theory (DFT). This is testimony to the advances that have been made in modelling real materials and chemical processes using quantum chemical methods.

When departments of Aeronautical and Mechanical Engineering hire people to work on quantum turbulence will be a real sign of a significant contribution.


  1. (Part 1 of 3)

    Hi Ross. I thought I’d take you up on your request to comment on your blog. When giving a general colloquium, it can be difficult to foresee all of the possible ways that statements might be interpreted, so your forum gives me a shot at trying to clear up some of the points that I was trying to make but that might have not come across like I had intended. While it probably is more efficient (and helpful for the audience) to have the chance to address questions during or after a talk, this blog is alternatively useful in that it’s sort of like having an extended colloquium – it seems like there’s never enough time to cover everything! Also, please forgive me if this post seems somewhat long – I’ll limit my responses to just a few of your comments that I’d like to address. So to get to your comments…

    As I mentioned in my talk, it’s not easy to clearly define turbulence in a way that everyone finds acceptable. I am certainly not a classical turbulence expert, and there’s a lot about the subject that I know virtually nothing about. So when it comes to defining turbulence, and particularly 2D turbulence, I prefer the characterizations offered by J. Sommeria in an excellent review article on 2D turbulence – I’d encourage you to have a look (in “New Trends in Turbulence”, Les Houches lectures, DOI: 10.1007/3-540-45674-0_8, p. 385, 2001). This formed the basis of the way I characterized turbulence in my talk and which you reproduced in your blog. I mention this in case you or any readers are interested in looking into this further. I particularly like Sommeria’s characterization because it encompasses phenomenology observable in both 3D and 2D.

    Regarding Kosterlitz-Thouless physics: you are right in thinking that this is quite different than what I presented in my talk! This is why I didn’t even mention the KT transition in my talk. KT physics has to do with characterizing equilibrium states of 2D quantum fluids. My talk was about non-equilibrium phenomena (specifically quantum turbulence). However, I think your interpretation that the dissociation of vortex dipoles that I alluded to is “just the Kosterlitz-Thouless transition” is not quite correct. More specifically, in a quantum fluid the dynamics of vortices and vortex dipoles depend on the presence of other vortices and on the trapping geometry. This can lead to dissociation of a vortex-antivortex pair. (Dissociation and vortex dipole annihilation can happen in 3D too.) Thermal activation of a vortex pair (ie, KT physics) is a different topic. Unfortunately I didn’t even think about discussing these differences in my talk - it would have been a great question during or after the talk. Thanks for the heads-up on this - I’ll watch out for this kind of misunderstanding next time.

    There’s one long but important point that I also think is worth mentioning, and that is the role of basic investigations in physics. To clear up something first: I’ll take this chance to emphasize (as I tried to do in my talk) that I do not think that we BEC physicists have yet made a significant advance when it comes to a microscopic understanding of classical turbulence (or even quantum turbulence), and I certainly would not claim to have made such an advance. The BEC community will be the first to tell you that BEC physicists have not helped engineers develop airplanes that can better deal with atmospheric turbulence or fluid dynamics engineers send oil through a pipe any more efficiently than they already know how to do. Nor have we BEC experimental physicists yet learned much about the quantum turbulence problem; the superfluid helium community has made much progress on that front in the last 50 years, and as I said in my talk, BEC experimentalists have just started seriously looking at this problem in the last year or so – there’s still so much left to do!


  2. (Part 2 of 3)

    With that said, here’s the intended take-home message of my talk: by studying BECs we have the potential to make new and unique advances in various areas (specifically turbulence, for this talk), but not that new advances (in turbulence, etc) have already been made by BEC physicists. Admittedly, the part of my slide that you reproduced in your blog makes my point seem somewhat ambiguous (I’ll amend it for next time), but I had hoped that my colloquium (and the rest of that slide) had made my take-home message clear. In more detail: I was trying to emphasize that atomic BECs are a new and potentially important platform for pursuing quantum turbulence work, and that they could also contribute to significant studies in other broadly important areas (such as phase transitions). Also, that just because we think of BECs as quantum “objects” doesn’t necessarily mean that we can only learn about the world of quantum mechanics by studying them – the “quantum and classical worlds” are just not that finely segregated (in my opinion). My talk was also partially aimed at explaining why the potential for advances exists with BECs – there are unique opportunities for setting up experiments, making measurements, and understanding the results theoretically (the last of which I unfortunately didn’t have time to do justice to). I tried to emphasize in my conclusions that I don’t yet know what a connection to classical turbulence will look like, and that anything I can envision on that front is far in the future and that I don’t see a clear path to get there – I illustrated point as a “cloud” representing the general turbulence problem in one of my last slides, disconnected from the BEC “foundation” that I had illustrated. There is such an important and enormous body of work that has gone into understanding turbulence that it’s hard to see how to make useful and significant progress on a microscopic understanding of turbulence – but I certainly do think we should try if we have an inkling of how this might be accomplished, and I would hope that the general turbulence community would welcome such efforts.

    For anyone reading your blog who didn’t attend my talk, I should make something clear: I did not state or imply that engineering departments should hire BEC physicists to solve their fluids engineering problems. But more importantly, I also disagree that a “real sign of a significant contribution” must be measured by an engineering department’s willingness to hire people (BEC physicists, say) to work on quantum turbulence. This is a fairly limited measure of the contributions of basic physics research to science and technology. We physicists should be the first to recognize the roles played by basic research, and not always be focused on the need to envision and work directly on all immediate applications. Still, it is important to recognize the potential motivations for our work. You’re probably familiar with the story of the laser as a solution in search of a problem when it was first invented 50 years ago – a fairly obvious example of how basic research leads to important and unforeseen discoveries without a specific commercial advance or application envisioned. For the case of turbulence that we’re considering, there’s a different example/analogy that I like even better:


  3. (Part 3 of 3)

    In the 1800’s, chemists knew how to work with gases and liquids in order to produce substances, burn materials, etc. The ideal gas law was known. A rudimentary internal combustion engine was even invented in the 1600s (C. Huygens). But even at the beginning of the 1900s there was still not an accurate or accepted microscopic theory of matter and atoms. Fortunately, the successes of chemistry and engineering applications didn’t stop physicists from pursuing atomic theory for its own sake. As far as I know, physicists did not say “our work will be deemed significant only once a chemistry department hires a physicist working on a microscopic theory of matter.” While recognizing that the study of matter could be motivated by chemistry, and could perhaps lead to advances in chemical engineering, engines (etc), the physicists of the early 1900s were likely more driven by the intellectual desire to understand the microscopic nature of matter for its own sake. With many years of progress without a specific vision or product in mind, the structure of the atom was finally uncovered – as was the development of quantum mechanics. The latter could not have been envisioned. There might have even appeared in someone’s chalk-talk in 1900 a picturesque “cloud” with “New theory of matter” written on it. But we all know that the development of quantum mechanics would not have occurred without the pursuits of physicists driven by the desire to deeply understand the nature of matter (and light). I can imagine the physicists of the late 1800s and early 1900s saying “maybe our work will lead to significant new understanding of the nature of the universe, with potential applications in chemistry and engineering.” A statement such as that might have been dismissed by chemists and engineers of the day saying “yeah, right”, but fortunately the drive for pure discovery persisted. (Actually, I tend to think that the chemists and engineers of the day may have welcomed such research – it seems like it would have made life more exciting for everyone.)

    Regarding work with quantum turbulence, the main message of my talk encompassed the notion that quantum turbulence work in BEC is worth pursuing for its own sake, and for the possibility that someday, in ways that we don’t yet envision, there may be advances that help illuminate the microscopic nature of even classical turbulence. If that’s the case, I think this avenue of research will prove to be significant even if an engineering department doesn’t see any need to hire BEC physicists.

    By the way, I do agree with your comment that “potential advances and hoped for insights” are not the same as real advances, although I personally would rephrase this as “the motivations to undertake an experiment should be distinguished from results of an experiment.” This may seem obvious to both of us, but there is another important point worth making: as educators (and colloquium speakers), I think it is important to show students that *motivation* is an important and unique element in the scientific process. There are many scientists that seem to be so focused on their own particular area of research that they don’t efficiently develop broad connections, insights, and motivations for pursuing their own work. They may even be fantastic at what they do, and the progress of science needs people like this (I think). But science also needs people that will push boundaries, develop new ideas, and unite previously disparate ideas. Scientific motivation is a hard thing to teach in a classroom, but at least by presenting and emphasizing motivations, grand visions, and possible applications without assuming the need to emphasize an actual immediate result, we can hope to get across the ideas that motivations are as important in science as solving equations. This is my opinion anyway.

    Thanks for the opportunity to respond to your comments!


    Brian P. Anderson

  4. Hi Brian,

    Thanks for your thoughtful response and engaging so thoroughly with my comments.

    You should take it as a compliment that I learnt so much from your colloquium and that it stimulated such a detailed post on my part.

    I agree with almost all of your points. I agree that engineering departments hiring physicists is not THE measure of a significant contribution. It is just A measure. Like you, I think physics research should be pursued for its own sake and its value should not be solely be measured by others outside the field. But, I am always impressed when a physicist makes such a significant contribution that they get hired by a non-physics department.

    I think if you modify your "take home point" slide as you suggest I and (perhaps other people) would be happy. This is consistent with the rule in talks to "never offer up undefendable ground" discussed here