Dated: 04/30/04
This proposal has been declined by NSF.

Comments from the cognizant Program Officer

Dear Dr. Cvitanovic:

Your proposal was reviewed by two panels: first, together with 44 other proposals by a panel of 11 experts in the areas of differential equations and applied dynamical systems, and subsequently together with 66 other proposals by a panel of 18 experts in the area of fluid dynamics.

Summary.

The proposal generated extensive discussions in the Applied Dynamical Systems panel. The panelists agreed that the PI had presented a novel approach to one of the fundamental problems of fluid dynamics. If successful, the results would have significant impact on fluid dynamics and its applications, for example in engineering. On the other hand, the panel had some serious reservations. The main reservation concerned the transition from a one-dimensional model (Kuramoto-Sivashinsky) to the full three-dimensional Navier-Stokes equations. Because the proposal was vague on details, the panelists felt that this gap was too wide to make the proposal truly believable. The consensus of the panel was that this was a high-risk proposal.

The proposal provoked much more critical reactions in the Fluids panel. The panelists agreed that the PI had addressed one of the fundamental problems of fluid dynamics, but they were considerably more sceptical about the likelihood of its success. The reviewers noted that the ideas were not new and that the PI had not made the connection with prior results. A serious objection was that it was not even clear what the results of the study would be and how the results would yield information about quantities of interest to the practitioners. One reviewer noted that the amount of computational work that would be required if the method were successful might be more than that of a direct numerical simulation. Also, the successful completion of the project would depend heavily on the participation of skilled collaborators, and it was not clear from the proposal that any of the possible collaborators listed had the required expertise. The panel recommended that the PI seek closer collaboration with a computational expert, as well as with experimentalists. The panel placed the proposal in the non-competitive category.

This proposal has merits, but the consensus seems to be that it carries a considerable element of risk. Some risk is fine, but the proposal needs to make a convincing case that it is worth taking the risk.

This proposal is concerned with identifying recurrence patterns as a means for studying turbulence in fluid mechanics. The panel expressed concern that the preliminary results achieved by the PI on the 1D KS equation would not necessarily translate to the 3D Navier-Stokes equations and it was suggested that perhaps a 2D example would be an appropriate middle step.

RATING: E,E,V
Recommendation: Highly competitive, recommend funding

The reviewers felt that it is an overly ambitious project and questioned the likelihood of achieving the stated objectives in three years. The plan was not sufficiently detailed. In particular, the PI did not explain how he was going to improve on several previous works along the lines proposed here, neither did he state in sufficient detail how he was going to proceed. The reviewers thought the PI might benefit from collaborations with researchers closely involved with practical applications of these methods to particular flow fields. This would significantly strengthen the proposal.

RATING: V,G,P
Recommendation: The panel rated this proposal "non-competitive".

If successful, the proposed research would yield a formidable toolkit for engineers involved in fluid dynamical problems: essentially, a way to control turbulent motion. Yet this reviewer remains skeptical about the feasibility of such program...

This proposal emphatically glorifies Hopf's dynamical view of the world, and optimistically proposes to carry out the program of reducing turbulent motion to a walk among recurrent patterns, from which much average information about the system could be in principle extracted. It does appear to this reviewer that there is a huge gap between seeing the first glimpse of the program's applicability to 1D KS, to carrying it through for 3D Navier-Stokes (and more so when this is to be done without any fluid dynamical input other than the equations.) Yet the PI's enthusiasm is contagious. Maybe fully acounting for the phase-space structure of KS would be enough of an achievement?

The intellectual merit of better understanding turbulent flows and being able to predict their characteristics can be well appreciated. The question is, what are potentially successful approaches to accomplishing this, at least in part. The principal investigator acknowledges the computationally impossible task of recording three-dimensional color patterns in flows and searching for recurrent patterns. To address this, a variational principle is proposed that makes use of a "guess" for a loop representing an approximation to the solution and then utilizes a variational method to drive this loop to the actual periodic orbit solution.

The research plan given is far too brief, and is merely presented as an outline. This cannot be used as a basis for judging the quality and likelihood of success of the plan. The flavor of the proposal is, therefore, too speculative. The progression from one spatial dimension to three seems premature. Why not apply these ideas to two-dimensional flows first? While is it well-understood that strictly two-dimensional flows cannot be truly turbulent, as there is no vortex stretching, a two-dimensional system is no less physical than a one-dimensional system (which does not even have vorticity). For example, an interesting starting point could be the relatively recent two-dimesional experiments using soap films and vertical, gravity-driven soap film channels.

A large collaborative group is envisioned. It is not clear whether the personnel listed have actually agreed to participate, should this project be funded (it is stated that "PI intends to ask...to join the project").

The approach presented is perhaps simply stated too ambitious. There is certainly nothing negative about a sound "non-traditional" approach that is sufficiently promising, but the experimental and computational effort that is apparently needed to carry out the recurrent patterns approach in three dimensions may very well exceed that of direct numerical simulations. There have been many attempts over the years to develop low-dimensional descriptions of complex turbulent flows, with mixed success. In addition to a better understanding of turbulence, what is really needed is a model that predicts transport properties and statistics. It is not clear how the information acquired in the course of the proposed project can provide this type of data, especially for strongly turbulent flows. It is also not clear at all what exactly will emerge from this program of research: for example, is the intent to arrive at some kind of system of ordinary differential equations that represent modes of fluid dynamic fields? How can the resulting "product" be used to estimate real turbulent quantities of interest to practical applications. [Material redacted per PAM Chapter XI G.2] Given the weaknesses of the proposal, the overall rating is poor. The intellectual merit is poor and the broader impacts are fair, overall.

This proposal ranks in the bottom third of those I have reviewed.

This proposal is about identifying patterns in turbulent flows, and building an understanding of such flows from that. The one-dimensional case, much easier since no topology is involved, will be a first testing ground, studying Kuramoto-Sivashinsky, and then the proponent wants to redo the numerical study of Kawahara and Kida (2001) on Couette flows.

Of course, the idea is not new; really, it dates back to the Lorenz attractor, when some people thougth that turbulence would be solved with chaotic temporal dynmics but (very) smooth spatial flows. Here, the idea is to increase the spatial complexity but still try to identify what could be the atoms of turbulence, to loosely paraphrase Lord Kelvin who was trying to do that with knots.

Of course, that idea (patterns) is not new either; we could start with van Dyke album of fluid motions, with EOF or POD techniques for which Nadine Aubry and others were pioneers; no reference is given to them, no bridge is done to these approaches; neither are quoted the people trying to identify patterns using wavelets (Marie Farge and others). I can think as well of early works by MacLaughlin and collaborators on the switching of between temporal and spatial complexity on one-dimensional equations, or of the study of patterns by Newell et al. in convection or optical turbulence, not to mention finance.

I am also a little surprised that topology is not part of this game; I think it should; topology (e.g. the study of knots, including wild knots) has proven useful in the study of DNA.

There is no doubt that, close to transition to turbulence, patterns occur in a strong way. The bulk of the work proposed is on Kuramoto-Sivashinsky (not turbulence in the classical sense) and on Couette flows, a step in the direction of turbulence. A collaboration with Kida and Kawahara, pioneers in this field (so is Waleffe, working also on Poiseuille flow) is indicated although not being part of the proposal. Collaborations with experimentalists and numericists is also indicated.

But that should not deter us from supporting this proposal. I put it in the second category.

The PI does not appear to have prior expertise to carry through the necessary sophisticated calculations of unstable time periodic solutions in the 3D Navier-Stokes equations. The successful completion of this research will therefore depend heavily on the participation of skilled collaborators. The PI lists a few possible collaborators at Georgia Tech but it is unclear whether any of them have the expertise to develop the necessary numerical codes. However, this is a novel proposal on one of the great open problems in fluid mechanics.

Rank: Middle third.