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Nonequilibrium Probability Currents in Optically-Driven Colloidal Suspensions

by Samudrajit Thapa, Daniel Zaretzky, Ron Vatash, Grzegorz Gradziuk, Chase Broedersz, Yair Shokef, Yael Roichman

Submission summary

Authors (as registered SciPost users): Yael Roichman · Yair Shokef · Samudrajit Thapa
Submission information
Preprint Link: https://arxiv.org/abs/2310.12718v1  (pdf)
Date submitted: 2023-10-20 12:00
Submitted by: Thapa, Samudrajit
Submitted to: SciPost Physics
Ontological classification
Academic field: Physics
Specialties:
  • Statistical and Soft Matter Physics
Approaches: Theoretical, Experimental, Computational

Abstract

In the absence of directional motion it is often hard to recognize athermal fluctuations. Probability currents provide such a measure in terms of the rate at which they enclose area in phase space. We measure this area enclosing rate for trapped colloidal particles, where only one particle is driven. By combining experiment, theory, and simulation, we single out the effect of the different time scales in the system on the measured probability currents. In this controlled experimental setup, particles interact hydrodynamically. These interactions lead to a strong spatial dependence of the probability currents and to a local influence of athermal agitation. In a multiple-particle system, we show that even when the driving acts only on one particle, probability currents occur between other, non-driven particles. This may have significant implications for the interpretation of fluctuations in biological systems containing elastic networks in addition to a suspending fluid.

Current status:
Awaiting resubmission



Reports on this Submission

Anonymous Report 3 on 2024-1-11 (Invited Report)

Report

The authors study two optically trapped colloidal particles that are hydrodynamically coupled due to the solvent. One particle is driven by switching the trap position. Considering the projected positions $x_i$ of both particles, the authors address the question of estimating probability currents through measuring the enclosed area of the trajectory, and from this the rate (AER) of area changes, in the plane spanned by both particle positions. This idea first appeared in a review (Ref. 4) and the authors now elaborate on this concept through experiments and simple analytical calculations.

Inferring entropy production or at least lower bounds to the entropy production is currently intensively studied in order to assess complex (living) systems driven away from equilibrium. While the authors admit that the “connection between the underlying activity in the system and its manifestation in the AER is not fully understood”, I’m still missing a discussion on the relation between AER and entropy production. The AER vanishes in equilibrium but is it supposed to be a bound? Does it equal the entropy production rate in some limit? What do I learn from quantifying the AER except that it is non-zero if the system is driven? Otherwise I feel this manuscript is sufficiently interesting for publication.

Further points:

- In the abstract, please reword “phase space”. Phase space denotes the space spanned by positions and momenta.

- On page 5, the authors write “with 30 nm spatial resolution”. Is that correct? That would be far below the optical resolution. I understand that the particles are µm and above the resolution threshold but still. What is the field of view and what is the pixel size? The scale bar in Fig. 1b is 50 nm, that would be about the error bar so that essentially the whole trajectory is of the order of the measurement error. It is hard to see how the authors estimate an error of 2 nm^2/ms for the AER?

- In Sec. V, the authors determine expressions for the AER, which is possible since they consider simple linear stochastic equations of motion. They then introduce hydrodynamic coupling through Eq. (15). However, it seems the coupled stochastic equations are solved for fixed $J$ [Eq. (18)] so that the positions fluctuate but the quantity $r$ is fixed (I suppose to the mean average?) and independent of the $\delta x$. This is a drastic simplification. The authors should at least attempt a Taylor expansion of the mobility tensor around $r$ and discuss whether the limitations of that approximation are consistent with the experiments.

  • validity: -
  • significance: -
  • originality: -
  • clarity: -
  • formatting: -
  • grammar: -

Anonymous Report 2 on 2023-12-24 (Invited Report)

Strengths

1) insightful minimal model
2) combines experiments and theory
3) well organised
4) wider applicability

Weaknesses

1)some potential issues with the derivation of the out of equilibrium hydrodynamically-coupled model
2) some parts of the model need to be clarified
3) parts of the text need to be specified better (see specific issues raised in the requested changes)

Report

The manuscript reports on the validation of the area-encoling-rate (AER) as a measure of out-of-equilibrium state in stochastic systems. The authors start with experiments focussing on the behaviour of a pair of colloidal particles held at distance “r” by separate optical tweezers (OTs). When particle 1 is actively driven by regularly displacing the position of its OT (typical size b0), the driving is felt also by particle 2 due to interparticle hydrodynamic coupling. The authors then observe the dynamics of the coupled system along the two dimensional projection of its phase space given by the coordinates (x1,x2) of the colloids along the line joining their average position. In the (x1,x2) space, the system’s position displays a net circulation around the point (avg(x1),avg(x2)) which can be quantified in terms of a AER. The experimental AER appears to be largely compatible with the results from simulations of the same system, showing a scaling with b0^2/r.
After analysing the experimental results, the authors lay down the general theoretical framework to analyse similar systems, with particles coupled either through hydrodynamics (dissipative coupling) or elastic coupling (conservative coupling).

Overall, I find the paper interesting and well organised. It provides good insights into the out-of-equilibrium behaviour of a simple model system, which can be of guidance for more complex cases. At the same time there are in my opinion a few issues that the authors need to address. Once these have been resolved satisfactorily, I will be happy to recommend the manuscript for publication.

Requested changes

The comments are ordered as the related text appears in the draft manuscript.

1) Pg.4. “[..] suspended in double distilled ionized water […]”.
I suspect there is a typo here.

2)Sec. Experimental Design. The authors should quantify the experimental error they expect for the parameters /tau and b0 of the driven optical tweezer. Amongst other things, this is important for example when discussing the plateauing observed at small b0 in the experimental points of Fig.4.

3)Sec. Experimental Design. As far as I can tell, the value of the parameter r/d is only found in the caption to Fig.1. Please make sure that this is explicitly stated in the main text of the paper.

4) Sec. Numerical Simulations. I am slightly puzzled by the choice of the Rotne-Prager approximation, rather than just the Oseen tensor, for the interparticle hydrodynamic interactions. Of course I agree that this is a better approximation in general. However, the correction term over the Oseen tensor is of the order (1/6)(d/r)^2, which is approximately 0.01 here (d being the diameter of the colloids). It does not hurt, but it also does not seem needed to me.

5) Sec. IV. When discussing the experimental values vs. the numerical values obtained either with the parabolic or the Gaussian approximations, it is clear that the agreement is better with the latter. However, later in the manuscript the authors also show that a finite-sampling-time can lead to an underestimate of the AER. Could this not be at play here as well? In other words, the *real* experimental AER could be closer to the parabolic traps’ case, with the difference only due to finite sampling time effects.

6) Sec. IV. Regarding the scaling of the AER with b0^2/r, perhaps one could already expect that as a simple consequence of hydrodynamic coupling. Given a typical displacement of particle 1 of “b0”, the typical displacement of particle 2 resulting from hydrodynamic coupling should be “b0 d/r” (d is the colloid radius). The area, then, will go like the product of the two, i.e. (b0^2)(d/r).

7)Sec. V, pg. 10. “governed by a Langevin equation with arbitrary coefficients”. It seems to me that Eq. (1) is actually a specific class of Langevin equations, rather than the most generic one.

8) Pg.11. “Equation 1 is quite general…”. Please be more specific.

9) Pg. 11. “A symmetric matrix V […] detailed balance”. It seems to me that requiring that the matrices V and D are mutually diagonalisable would be sufficient and more general than what is currently written in the text.

10) Pg. 13. “Note that the AER is independent of the distance […] motion”. I am not sure why this would be surprising. It appears to be a direct consequence of the assumption that all the couplings here are perfect Hookean springs. Under this assumption, the forces bear no dependence on the actual distance between the colloids, but only on the variation of this distance. Then it is not surprising that also the AER is independent of the interparticle separation.

11) Pg. 14, Eq.15. In reference also to point number 4) above, the tensor used here is the Oseen tensor. I am not sure why the authors introduce the Rotne-Prager approximation.

12) Pg.15, Eqs.17,18. I agree with the authors’ previous formulae on the elastically coupled colloids. However, I am not sure I agree with their approach in this case. I will try to explain myself. Please bear with me as it is a bit long to write it down. I hope it will be clear.

The system leading to Eq. 18 has

-particle 1, temperature T+\DeltaT
-particle 2, temperature T

Let us call this system, system 0.
The current analysis should be valid independently of whether \DeltaT is positive or negative. In particular, if instead of \DeltaT we take -\DeltaT, and have the following system (system 1)

-particle 1, temperature T-\DeltaT
-particle 2, temperature T

then the diagonal terms of the tensor D should be equal to those in Eq.18, with the sign of \DeltaT inverted:

D11= T- \DeltaT
D22= T-J^2\DeltaT

Now let’s go back and consider the original system (system 0), but define (T+\DeltaT) as T*:

T*=T+\DeltaT.

Then particle 1 is at temperature T* and particle 2 at temperature (T*-\DeltaT). Let’s now relabel particle 2 as particle 1*, and particle 1 as particle 2*. Then the complete “star” system (system 0*) is

-particle 1*, temperature T*-\DeltaT
-particle 2*, temperature T*.

According to the prescription above, the tensor D for this system should have diagonal terms

D1*1* = T*- \DeltaT
D2*2* = T*-J^2\DeltaT

However, the systems 0 and 0* are actually the same system, implying that D1*1* should be equal to D22 and D2*2* should be equal to D11. This is clearly not the case.

In other words, having particle 1 at \DeltaT with respect to particle 2, should be equal to having particle 2 at -\DeltaT with respect to particle 1. This does not seem to be the case here.
In my opinion, this problem arises from Eq.17. I do not think that Eq. 17 is correct. The correct form should be such that, if we consider T to be the average temperature and have particle 1 at temperatures T+0.5\DeltaT and particle 2 at temperatures T-0.5\DeltaT, then the two particles are treated in an equivalent way.
In other words, the system is not out of equilibrium because particle 1 is at temperature \DeltaT above particle 2, but because the two particles do now have the same temperature.

This problem persists in later parts of the manuscript and should be addressed there as well.

13) Pg.15. Given the tensor D, the tensor F is chosen by the authors through a Cholesky decomposition. However, what we know of the two tensors is simply that D=0.5FF^T. The particular choice of the Cholesky decomposition of D is but one of infinitely many choices one can make for the tensor F. For example, for any rotation matrix O, (FO) is also a perfectly fine choice… but it will give rise to a different “microscopic” dynamics.
This of course is due to the fact that, whilst there is one Fokker-Planck equation that can be derived from any Langevin equation, the opposite is not true. There are infinitely many Langevin equations that give rise to the same Fokker-Planck equation. The authors should be more careful when presenting this part in their paper. The prescription they have used is valid, but is not unique. (Of course the AER is independent of the actual choice of F as long as 0.5FF^T=D)

14) The authors have looked at systems of 2 and 3 particles, and thanks to their analysis it is reasonably straightforward now to generalise the results to more particles (although the calculations might be tedious). However, I was wondering whether the authors could comment about the case of a single particle. Is there a simple way to test its potential out of equilibrium state using an AER-like measurement?

  • validity: high
  • significance: high
  • originality: high
  • clarity: high
  • formatting: perfect
  • grammar: good

Anonymous Report 1 on 2023-12-22 (Invited Report)

Strengths

1- This is an interesting paper on a central issue of stochastic thermodynamics: the investigation of probability currents in out-of-equilibrium systems, with the goal of quantitatively distinguishing these systems from their equilibrium counterparts.

2- The authors combine experiments, numerical simulations and theory to make their points.

3- The readability of the paper is very good. It is clear what the authors did (and did not do), and results obtained from previous papers are well referenced.

Weaknesses

1- The structure of the paper is suboptimal. Each part is dedicated to a different topic and the links between them are minimal. The overall consistency could be improved.

2- The paper often deviates from its main message and the link between the different theoretical parts (two temperatures, colored noise, three particles) and the experiments is sometimes hard to understand.

3- The scalings from the experimental data in Figs. 4 and 5 are not so convincing.

3- Some numerical observations are left unexplained (strong influence of the shape of the potentiel and the acquisition rate) even at a qualitative level.

4- The importance of looking at the AER, vs other observables, is not explained enough.

Report

Out-of-equilibrium systems exhibit probability currents that may be challenging to measure, especially in experiments. In this article, the authors put forward (i) a model experimental system: beads trapped by optical tweezers with a stochastic repositining of one trap at equally spaced times and (ii) a measure of probability currents: the area enclosing rate (AER). They additionally perform numerical simulations (Stockesian dynamics) and theoretical computations of the AER in simple cases.

I nevertheless find this article not entirely convincing since the experimental scalings are unclear, the most puzzling numerical observations are not explained so well, and the numerous theoretical models could be better connected to the experiments. In short, I am currently not in favor of the publication of this article in SciPost Physics as it is now. But I do believe it has a good potential and I encourage the authors to improve it and resubmit.

I list several questions and comments below. Some other points are listed in "Weaknesses" and "Requested changes" and will not be repeated here.

1- One point that puzzles me in the article is that on the one hand the theory (sections VI and VII) is done at the linear order in displacements ; while on the other hand the simulations show that non-linear effects (Gaussian traps) change the AER by one order of magnitude. Do the authors have any idea why the non-linear effects are so strong, and how they can be explained, at least qualitatively.

2- In the discussion, "We also demonstrate that the AER peaks when the driving time scale $\tau$ is comparable to the relaxation time scale $\gamma/\tau$". I'm sorry but I do not see what part of the main text is dedicated to this issue.

3- Why did the authors choose a frequency $1/\tau=36$ Hz? How do the results depend on this frequency?

4- Fig. 3b gives the fealing that the plateau is almost at zero. Maybe the $y$ range can be made smaller (or error bars included).

5- What would be a derivation for the potential $U(x)$ used at the top of page 9 for a Gaussian beam (reference?)? Also, shall I understand from the values that $w\sim \lambda/2$?

6- What is the status of section V? Is it a reminder of known results? A warm-up before the following section? Some new computations related to AER?

7- Is there is qualitative link between the two-temperature problem and the colored noise problem? For instance an approximate mapping? Or are they two separate out-of-equilibrium issues?

8- Is there a reason to use the Cholesky decomposition, as opposed to the (symmetric) square root of a symmetric matrix? Do both lead to the same results?

9- Eq. (14), maybe say that the $1/r^3$ term will be neglected in the following, since it is never used.

10- I think the rational for section VIII could be made clearer, since it is not (directly) connected with the experiments.

Let me end this report by saying that I shall be supportive if the authors experience difficulties to resubmit due to the current situation in their country.

Requested changes

1- Add an outline at the end of the introduction to introduce and show the consistency between the different parts.

2- Refactor the whole article so that the message is clear throughout and that the sections are better linked with one another. This may involve moving some of the theory into appendices.

3- Give more details earlier in the text about what the AER is, for which pair of variables it may be computed, why it is important and what alternative observables could have been considered. Giving some basic theoretical results (such as Eq 6) earlier may help.

4- Be clearer (and more honest) about what can be deduced from the experimental data. Why do the authors think that the scalings from the simulations are also seen in experiments (Figs 4, 5)? To which degree of certainty? Maybe explain why the noise level and the error bars are quite large. If needed, additional experimental data may be shown in appendices.

5- Better comment the results of the simulations even when analytical results are not available. End of IV, is there any insight why the difference is so large when the shape of the trap is changed? End of VII, what happens between $10^4$ and 120 fps, why is the difference so large, how does it depend on the framerate ?

6- Give more details about the numerical simulations. Which framework is used (homemade or standard one), how is the code implemented ? Alternatively the authors may consider open-sourcing their code (github / Zenodo).

7- "s" is the standard SI symbol for "second", not "sec" [see https://www.bipm.org/en/measurement-units/si-base-units]. This should be corrected.

  • validity: good
  • significance: good
  • originality: good
  • clarity: high
  • formatting: reasonable
  • grammar: excellent

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