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Review of “Optimizing the Martini 3 force field reveals the effects of the intricate balance between protein-water interaction strength and salt concentration on biomolecular condensate formation” by Gül H. Zerze

Reviewed by F. Emil Thomasen and Kresten Lindorff-Larsen

Comment:

The preprinted manuscript by Zerze reports on molecular dynamics simulations of the intrinsically disordered low complexity domain (LCD) of FUS using a beta version of the coarse-grained force field Martini 3. The author performed simulations to study the formation of FUS LCD condensates under varying protein-water interaction strengths (in the Martini force field) and at different NaCl concentrations, and concludes that strengthening protein-water interactions by a factor of 1.03 improves the agreement with experimental transfer free energies between the dilute and dense phases. Additionally, the author concludes that the NaCl concentration affects condensate morphology and protein-protein interactions in the condensate, and that the effect of NaCl concentration on protein-protein interactions in the condensate is sensitive to rescaling of the protein-water interactions. The preprint provides an interesting and novel benchmark of the (beta) Martini 3 model in predicting phase separation of IDPs, and reveals potential short-comings of the model in predicting protein concentrations in (or volumes of) the condensed and dilute phases. This benchmark will be useful for readers who wish to simulate liquid-liquid phase separation of IDPs with Martini 3, and the work will be interesting to a wider audience interested in the biophysics of IDPs and their condensates.

Below we outline some questions and comments that the author might take into account when revising the manuscript. Our main comment regards a clearer assessment of the convergence of the simulations and correspondingly the lack of error estimates for observables calculated from the simulations. We also suggest a clearer presentation of the experimental data used to validate the simulations. While some of these changes are mostly textual, in other cases we suggest additional simulations. We realize that some of these simulations require substantial resources; if these are beyond what is available, we suggest at least to clarify caveats as per the points below.

We have the following suggestions for revisions to the manuscript:

1)

Fig. 1 and 2: The finding of non-spherical droplets is interesting and intriguing. To examine whether the formation of these shapes in the simulations with higher salt and λ-values represent stable states or perhaps trapped metastable states of the system, we suggest that:

1a) The author runs simulations with the parameters that give rise to non-spherical morphologies (e.g. λ=1.025 and 50 mM NaCl) starting from the structure of the spherical droplet (for example formed with λ=1.0 and no salt) and observe whether the non-spherical morphology is recovered or the droplet remains stable. If the droplet remains stable, then the effect of salt concentration on the inter-chain contacts (Fig. 6) could be assessed without potentially confounding factors from different dense phase morphologies.

1b) The author shows time-series or distributions of an observable that reports on the dynamics of the proteins in the non-spherical droplet (e.g. Rg, mean square displacement, residue-residue contacts) and/or of an observable that reports on the dynamics of the droplet shape (e.g. the x-, y-, and z-components of the gyration tensor).

1c) Additionally, independent replicas of droplet formation for each condition and parameter set would be ideal, but we realize that this would be expensive in computational resources and may be infeasible.

2)

“As λ increases, the volume of the dense phase increases (and condensed phase concentration decreases accordingly) until the system is not capable of forming a dense phase (λ >1.03)”: From Fig. 1 it seems that the rate of cluster formation decreases as λ increases. Is it not then possible that droplet formation at λ>1.03 is stable at equilibrium, but occurs on time-scales greater than those tested in the simulations? To support the statement that no droplets are stable at λ>1.03, we suggest that the author runs simulations with a higher value of λ starting from the structure of the spherical droplet (formed with λ=1.0 and no salt) to observe whether the droplet is dissolved or remains stable.

3)

Figure 3: The use of the radial distribution does not seem ideal for the droplets that have a non-spherical morphology, as certain distances will report on an average over the dense and dilute phases. This should at a minimum be discussed.

4)

Table 1: It seems that the discrepancy between the sigmoidal fit approach and the surface reconstruction approach increases with λ, possibly due to sensitivity to the shape of the droplets, illustrating that there might be significant uncertainty associated with the reported dense phase volumes. We think it would be useful to have an error estimate for the reported dense phase volumes (e.g. an error over volume calculation approaches and/or over different probe sizes).

5)

Table 2 and Fig. 4: We suggest that the author more explicitly states which experimental data was used for comparison with the simulations in Fig. 4. We also suggest a more direct comparison with experimental data points where possible (e.g. by showing the experimental values of csat as a function of NaCl concentration).

6)

“We used the “tiny” bead type (TQ1) both for Na+ and Cl- ions”: The author should clarify the reason for and possible effects of choosing the TQ1 bead type, as TQ5 is, we think, the standard bead type for Na+ and Cl- ions in Martini 3.

7)

We suggest that the author, where possible, reports error estimates for the various observables, for example from block error analysis and/or repeated simulations.

8)

It would be useful to include a discussion of the effects of simulation convergence and simulation starting configurations on the reported results.

9)

A discussion of the potential differences in the effect of non-bonded cut-offs in the dilute and dense phase would also be useful.

10)

It would be very useful if the inputs/settings (including starting configurations) used for simulation and code for analysis were available.

We also have the following suggestions for minor revisions to the manuscript:

1)

“We kept the protein-protein interactions unmodified (and no additional elastic backbone constraints were applied)”: The author should clarify whether this includes assignment of secondary structure and/or side chain angle and dihedral restraints (ss and scfix in Martinize).

2)

“All simulations were performed using GROMACS MD engine (version 2016.3).”: Error in references.

3)

In the Cluster Formation Analysis section: We suggest that the author cites the specific package used (e.g. SciPy).

4)

Fig. 2: There are small red dots on the droplets, which should either be explained in the figure text or removed.

5)

Fig. 3: It would be useful for the reader if the NaCl concentration was labelled at the top of each column. Additionally, the radial distribution of the ion concentration is shown as two separate rows, which we assume corresponds to Na+ and Cl- ions. This should be clearly labelled.

6)

“We found the largest water fraction For the ionic species…”: Typo?

7)

Fig. 4: Depending on how the plot is updated with more details on the experiments, perhaps the range shown on the y-axis could be made smaller.

8)

Fig. 5: May be clearer with a colourmap with three colours, as in figure 6.

Competing interests

The author declares that they have no competing interests.