Excerpted here are

Proposal Title | Turbulence: a walk through a space of unstable recurrent
patterns |

NSF Division | Division of Mathematical Sciences |

Program Name | APPLIED MATHEMATICS |

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.