The first attempt to submit NMRlipids II publication was postponed due to the extensive discussion and new contributions. The manuscript is again quite close to the submittable version (in my opinion). The results and discussion section has been rewritten but the conclusions and introduction are not essentially changed.
In the previous submission attempt I suggested the submission to Chemical Science for the same reasons as we submitted NMRlipids I to JACS (see discussion in Towards first submission to journal post). However, the publisher policies have changed quite a bit within one and half year so the discussion seems to be outdated. The RSC policies seems to officially allow this kind of work, thus there is no reason to test this anymore. For this reason, I suggest that we will submit to Physical Chemistry Chemical Physics (PCCP) where the acceptance is more likely.
There is still a ToDo list in the manuscript which mainly relates to missing technical information.
At some point we also need the Table of Content Graphics. I have opened the GitHub issue on that, please let us know if you have any suggestions.
If there will be no objections or major comments, I will proceed with the submission to PCCP within two weeks from now (13th of June 2016). Please, give all the comments and contributions before that.
Hi,
ReplyDeletehere are some comments on the current version. Some are very small (on the text), others not so small (I guess I have not understood stuff).
- in a couple of points in the text I find "bar Li+"; what is it?
- it took me a while to understand that there is a difference between the ion concentration and the bound charge. This is explained poorly and late in the text, in my opinion. I find it very confusing.
- equation 1 and 2 (which are the same, not sure why it's necessary to have them both): what is X (bound charge)? is it measurable? how? the reference cited [43] is not published, as far as I can tell. Does the equation come from theory or is it empirical? I guess it's the first, but this is not explained at all.
- More in general, I do not understand what is the proof of the electrometer concept. This is not good, considering that the entire paper tries to check whether different models fit this concept and the parameters of this equation.
- figure 2, the large decrease with CHARMM arises from longer equilibration: does that mean that the other simulations are not equilibrated? or that we don't know if we sampled an equilibrium in any simulation, including this one? This sounds bad. I hope I did not understand this.
- figure 4 is cited before figure 3.
- question 3 in the text: I'm fine with no reference at all. They have been cited and explained in the intro anyway, at least part of the relevant cases. I'm also fine if you decide to add references, I have no strong opinion on this.
- figure 7: which part of the simulations would be good for averaging? I'd say none, in both cases - no evidence that equilibrium is reached.
- at one point (page 5, right column) it is mentioned that CHARMM FF gives the highest affinity for Ca2+ because almost all cations are bound; some data is shown on figure 7 for 2 FFs, but no data is shown for all other FFs.
- in many parts of the text I find very long compound names, which are difficult to understand. "alpha and beta segment order parameter changes", come on! :-) "Changes in the order parameter of the alpha and beta segments" can be understood much more easily.
- Conclusions: "more careful studies and model development on lipid bilayer–charged object interactions are needed to make molecular dynamics simulations directly usable in physiologically relevant electrostatic environment." This sounds like saying that the 500 papers per year published with MD simulations of membrane systems don't say anything relevant for physiological conditions, no matter what their focus is. Sounds "a bit" strong. I suggest rephrasing, to point out more precisely the problems with MD simulations. Or, since you already said that, maybe this sentence is redundant.
- I found a bunch of small English imperfections, but did not correct them because I'd like to see a response to bigger points above, for now.
Luca
in a couple of points in the text I find "bar Li+"; what is it?
DeleteSee bar (preposition).
figure 2, the large decrease with CHARMM arises from longer equilibration: does that mean that the other simulations are not equilibrated? or that we don't know if we sampled an equilibrium in any simulation, including this one? This sounds bad. I hope I did not understand this.
DeleteI guess we don't know for sure if we sampled an equilibrium in any simulation, but at least for C36 we know that the Ca++ the binding times are very long, see Matti's comment, and especially Samuli's reply to it.
I have now made clarifications based on comments by Luca, see https://github.com/NMRLipids/lipid_ionINTERACTION/commit/45987cea2847ff81df42f0e738898307a33299b4
DeleteMore detailed replies here:
LUCA: "- in a couple of points in the text I find "bar Li+"; what is it?"
Since this seems to create some confusion, I have changed this to except now.
LUCA: "- it took me a while to understand that there is a difference between the ion concentration and the bound charge. This is explained poorly and late in the text, in my opinion. I find it very confusing."
I am not quite sure what you did not understand, but the section II A has been clarified now. Please check if you understand now or specify the unclarities.
LUCA: "- equation 1 and 2 (which are the same, not sure why it's necessary to have them both): what is X (bound charge)? is it measurable? how? the reference cited [43] is not published, as far as I can tell. Does the equation come from theory or is it empirical? I guess it's the first, but this is not explained at all."
The reason to have Eq. 2 is that the change \Delta S_{\rm{CH}}^{i} is defined there. I believe that it serves, for example, a reader who is looking Fig. 2 without reading the text and wants to find out what is in y-axis. Thus, I think we should keep it.
X is the amount of bound charge per lipid. This can be measured but details depend on the system. This is quite extensively discussed in the cited references so I think we should not start to repeat this here.
The reference which was [43] (now [39]) is now published (http://dx.doi.org/10.1021/acs.langmuir.6b00788). The reason why it is cited here is that, in principle, there are couple of potentially non-trivial steps when transforming this equation from quadrupolar splittings to C-H order parameters. These steps are discussed in that reference. To simplify the manuscript I decided not to repeat these steps but only write the result.
Please check the current version of the II A section. These issues are now clarified there.
LUCA: "- More in general, I do not understand what is the proof of the electrometer concept. This is not good, considering that the entire paper tries to check whether different models fit this concept and the parameters of this equation."
This is described in the first paragraph of II A section. The real proof is extensively discussed in the references and there is no reason to repeat it here. The section II A has been clarified now. Please check if you understand now or specify the unclarities.
(continues)
(continues)
DeleteLUCA: "- figure 2, the large decrease with CHARMM arises from longer equilibration: does that mean that the other simulations are not equilibrated? or that we don't know if we sampled an equilibrium in any simulation, including this one? This sounds bad. I hope I did not understand this."
The related discussion is in Supplementary information (Appendix A).
The last sentences are:
"The results suggest that in other simulations the binding affinity is underestimated due to the insufficient equilibration
times. This should be taken into account in more careful studies, but do not interfere the conclusion in this work
that Ca2+ binding is most likely overestimated in all the other models than CHARMM36 with ion model by Yoo et al. [73]."
LUCA: "- figure 4 is cited before figure 3."
Fixed.
LUCA: "- question 3 in the text: I'm fine with no reference at all. They have been cited and explained in the intro anyway, at least part of the relevant cases. I'm also fine if you decide to add references, I have no strong opinion on this."
Ok.
LUCA: "- figure 7: which part of the simulations would be good for averaging? I'd say none, in both cases - no evidence that equilibrium is reached."
The relevance of this for the current manuscript is discussed in the Appendix A, see also quotation above.
LUCA: "- at one point (page 5, right column) it is mentioned that CHARMM FF gives the highest affinity for Ca2+ because almost all cations are bound; some data is shown on figure 7 for 2 FFs, but no data is shown for all other FFs."
This can be seen from the density plots in Fig. 6; the Ca2+ concentration in water is nearly zero for CHARMM36 which is not the case for other models.
LUCA: "- in many parts of the text I find very long compound names, which are difficult to understand. "alpha and beta segment order parameter changes", come on! :-) "Changes in the order parameter of the alpha and beta segments" can be understood much more easily."
Please specify the locations of unclear text (note also that there are quite a lot of updates done recently).
LUCA: "- Conclusions: "more careful studies and model development on lipid bilayer–charged object interactions are needed to make molecular dynamics simulations directly usable in physiologically relevant electrostatic environment." This sounds like saying that the 500 papers per year published with MD simulations of membrane systems don't say anything relevant for physiological conditions, no matter what their focus is. Sounds "a bit"
strong. I suggest rephrasing, to point out more precisely the problems with MD simulations. Or, since you already said that, maybe this sentence is redundant."
This sentence reads now:
"more careful studies and model development on lipid bilayer--charged object interactions are called for to make molecular dynamics simulations directly usable in a physiologically relevant electrolytic environment."
We have shown that the binding of Na is not correct in most models and Ca binding is not correct in any of the models. Both ions are present in physiological electrolytic environment. Consequently, there is no model available where you could put bilayer with physiological electrolytic environment and directly use it for scientific studies without very careful and complicated interpretation. Thus, I think that this sentence is not too strong.
Luca Monticelli send me some comments by email, see
ReplyDeletehttps://github.com/NMRLipids/lipid_ionINTERACTION/blob/master/scratch/LIPIDionINTERACTlucaCOMMENTS.pdf
https://github.com/NMRLipids/lipid_ionINTERACTION/blob/master/scratch/LIPIDionINTERACTsupplLUCAcomments.pdf
I have now implemented the suggested changes and below are responses on some comments about supplementary information.
Comment about supplementary information, section 1, sentence
"The results show clear increase in binding affinity up to 1000 ns and 700 ns in CHARMM36 and Slipids"
MONTICELLI:
The binding affinity is a thermodynamic quantity and cannot change in time. The change seen in the plot is "instantaneous" amount of ions bound to the lipids, hence it is not a thermodynamic quantity.
OLLILA:
I have changed te "binding affinity" to "ion binding" when Fig. S1 is referred.
Comment about supplementary information, section 1, sentence
"The results suggest that in other simulations the binding affinity is underestimated due to the insufficient equilibration times."
MONTICELLI:
I don't think so, as we don't show any trends for the other simulations. It may even be that they start with fully bound ions and then the amount of bound ions decreases - I know nothing on the starting configurations and how they evolve, there is no info on this in the paper.
OLLILA:
The generation of starting configurations are described in the Methods section. Typically ions are added by replacing random water molecules with ions. It is very unlikely that ions would be fully bound in this kind of starting configuration. Anyway, I have softened this sentence by changing "is underestimated" to "may be underestimated".
Comment about supplementary information, section 2, sentence
"Three limits were tested: until the g3-carbon (Fig. S2), until the phosphorus (Fig. 3 in the main text), and until the a-carbon (Fig. S3) density maximum."
MONTICELLI:
The measure used here seems rather rough. Wouldn't it be possible to just integrate the oxygen-ion RDF until the first minimum after the peak? [To be precise, the same should be done for all oxygens in the lipids, and then the results should be summed up] This is what is often done in simulations, and it makes perfect sense (although I agree that a certain amount of arbitrariness remains)
As a simpler alternative, one can look at a few RDFs and decide a cutoff distance (e.g., distance of the first minimum, supposing that it is always about the same, for all oxygen-ion pairs), then count the number of ions within that distance from any oxygen at any given time.
OLLILA:
This analysis was little bit discussed in the blog, see discussion starting from http://nmrlipids.blogspot.com/2015/12/towards-submission-of-nmrlipids-ii.html?showComment=1451396890293#c659800953367200201
As pointed out also in that discussion, there would be also other alternatives for the analysis. However, I think that the only way to get fully rid of ambiguity is to have a simulation model which reproduces the experiments and use that to define which ions can be considered as "bound" and which not. Also the analysis suggested here is not very simple and the currect analysis in the manuscript serves the current conclusions pretty well. Thus I think we should leave these attempts for future studies. I assume that you are referring that rdf's are often used to analyze contacts between single atoms, not on ion binding analysis on lipid bilayer in the suggested way. But if there really is literature where the ion binding on lipid bilayers is calculated in such a way, let us know.
CONTINUES
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DeleteComment about supplementary information, section 3, first paragraph
MONTICELLI:
but then, why would those charged amphiphiles have the same effect on the alpha and beta order parameters as free ions? the binding of amphiphiles will most likely be different, as they are restrained in the positions they can assume in the bilayer - contrary to ions, which can go anywhere in the bilayer. I have a hard time seeing a direct relationship between free ions and bound detergents, I don't see why they should have the same effect on order parameters; and if they do have the same effect, then I don't see a clear molecular interpretation. Maybe it's just me, but I suggest that you try to explain this better.
OLLILA:
From the electrometer literature it is know (based on empirical observations) that all the charged objects have pretty similar effect on the alpha and beta order parameters (for more details see Ref. 36 and 38). I did add a mention on this in the beginning of section 2.1 in the main text:
"The molecular electrometer concept is based on the experimental observation that binding of any charged objects (e.g. ions, peptides, anesthetics, amphihiles) on a PC bilayer interface induces systematic changes in the choline"
There are some differences in details (like m_i slopes) but the main effect is the same. As written in the main text
"...This can be rationalised by electrostatically induced changes in choline P--N dipole tilt \cite{seelig87,scherer89,seelig90}..." .
However, there would be room for more studies here. In principle, simulations could produce the effect on bound ions correctly even thought the response on amphiphiles is not exactly correct (this would not matter for the current conclusions). Also opposite scenario is, in principle, possible. As discussed in the manuscript there is also some difference between different amphiphiles arising from unknown reason. Also, reading the Ref. 7 carefully one can see that the response slightly depends on amphiphile acyl chain length (very small but systematic and measurable difference). To tackle the issues more carefully, we would need some more simulation data with the same charged amphiphiles used in the experiments. However, we have to leave this for future studies now. Even though some of these details might, in principle, somewhat affect our conclusions I find it quite unlikely. I think that many of these issues would be pretty much solved if we would have a MD model which would reproduce the NMR data, thus I think we should focus on finding such a model.
The manuscript is now submitted to Physical Chemistry Chemical Physics.
ReplyDelete