Conformational dynamics of a nicotinic receptor neurotransmitter binding site

Reviewer #1 (Public Review):

Summary:

The authors want to understand fundamental steps in ligand binding to muscle nicotinic receptors using computational methods. Overall, although the work provides new information and support for existing models of ligand activation of this receptor type, some limitations in the methods and approach mean that the findings are not as conclusive as hoped.

Strengths:

The strengths include the number of ligands tried, and the comparison to the existing mature analysis of receptor function from the senior author's lab.

Weaknesses:

The weakness are the brevity of the simulations, the concomitant lack of scope of the simulations, the lack of depth in the analysis and the incomplete relation to other relevant work. The free energy methods use seem to lack accuracy - they are only correct for 2 out of 4 ligands.

Reviewer #2 (Public Review):

Summary:

The aim of this manuscript is to use molecular dynamics (MD) simulations to describe the conformational changes of the neurotransmitter binding site of a nicotinic receptor. The study uses a simplified model including the alpha-delta subunit interface of the extracellular domain of the channel and describes the binding of four agonists to observe conformational changes during the weak to strong affinity transition.

Strength:

The 200 ns-long simulations of this model suggest that the agonist rotates about its centre in a 'flip' motion, while loop C 'flops' to restructure the site. The changes appear to reproduced across simulations and different ligands and are thus a strong point of the study.

Weaknesses:

After carrying out all-atom molecular dynamics, the authors revert to a model of binding using continuum Poisson-Boltzmann, surface area and vibrational entropy. The motivations for and limitations associated with this approximate model for the thermodynamics of binding, rather than using modern atomistic MD free energy methods (that would fully incorporate configurational sampling of the protein, ligand and solvent) could be provided. Despite this, the authors report correlation between their free energy estimates and those inferred from experiment. This did, however, reveal shortcomings for two of the agonists. The authors mention their trouble getting correlation to experiment for Ebt and Ebx and refer to up to 130% errors in free energy. But this is far worse than a simple proportional error, because -24 Vs -10 kcal/mol is a massive overestimation of free energy, as would be evident if it the authors were to instead to express results in terms of KD values (which would have error exceeding a billion fold). The MD analysis could be improved with better measures of convergence, as well as more careful discussion of free energy maps as function of identified principal components, as described below. Overall, however, the study has provided useful observations and interpretations of agonist binding that will help understand pentameric ligand-gated ion channel activation.

Main points:

Regarding the choice of model, some further justification of the reduced 2 subunit ECD-only model could be given. On page 5 the authors argue that, because binding free energies are independent of energy changes outside the binding pocket, they could remove the TMD and study only an ECD subunit dimer. While the assumption of distant interactions being small seems somewhat reasonable, provided conformational changes are limited and localised, how do we know the packing of TMD onto the ECD does not alter the ability of the alpha-delta interface to rearrange during weak or strong binding? They further write that "fluctuations observed at the base of the ECD were anticipated because the TMD that offers stability here was absent.". As the TMD-ECD interface is the "gating interface" that is reshaped by agonist binding, surely the TMD-ECD interface structure must affect binding. It seems a little dangerous to completely separate the agonist binding and gating infrastructure, based on some assumption of independence. Given the model was only the alpha and delta subunits and not the pentamer with TMD, I am surprised such a model was stable without some heavy restraints. The authors state that "as a further control we carried out MD simulation of a pentamer docked with ACh and found similar structural changes at the binding pocket compared to the dimer." Is this sufficient proof of the accuracy of the simplified model? How similar was the model itself with and without agonist in terms of overall RMSD and RMSD for the subunit interface and the agonist binding site, as well as the free energy of binding to each model to compare?

Although the authors repeatedly state that they have good convergence with their MD, I believe the analysis could be improved to convince us. On page 8 the authors write that the RMSD of the system converged in under 200 ns of MD. However, I note that the graph is of the entire ECD dimer, not a measure for the local binding site region. An additional RMSD of local binding site would be much more telling. You could have a structural isomerisation in the site and not even notice it in the existing graph. On page 9 the authors write that the RMSF in Fig.S2 showed instability mainly in loops C and F around the pocket. Given this flexibility at the alpha-delta interface, this is why collecting those regions into one group for the calculation of RMSD convergence analysis would have been useful. They then state "the final MD configuration (with CCh) was well-aligned with the CCh-bound cryo-EM desensitized structure (7QL6)... further demonstrating that the simulation had converged." That may suggest a change occurred that is in common with the global minimum seen in cryo EM, which is good, but does not prove the MD has "converged". I would also rename Fig.S3 accordingly.

The authors draw conclusions about the dominant states and pathways from their PCA component free energy projections that need clarification. It is important first to show data to demonstrate that the two PCA components chosen were dominant and accounted for most of the variance. Then when mapping free energy as a function of those two PCA components, to prove that those maps have sufficient convergence to be able to interpret them. Moreover, that if the free energies themselves cannot be used to measure state stability (as seems to be the case), that the limitations are carefully explained. First, was PCA done on all MD trajectories combined to find a common PC1 & PC2, or were they done separately on each simulation? If so, how similar are they? The authors write "the first two principal components (PC-1 and PC-2) that capture the most pronounced C. displacements". How much of the total variance did these two components capture? The authors write the changes mostly concern loop C and loop F, but which data proves this? e.g. A plot of PC1 and PC2 over residue number might help?

The authors map the -kTln rho as a free energy for each simulation as function of PC1 & PC2. It is important to reveal how well that PC1-2 space was sampled, and how those maps converged over time. The shapes of the maps and the relative depths of the wells look very different for each agonist. If the maps were sampled well and converged, the free energies themselves would tell us the stabilities of each state. Instead, the authors do not even mention this and instead talk about "variance" being the indicator of stability, stating that m3 is most stable in all cases. While I can believe 200ns could not converge a PC1-2 map and that meaningful delta G values might not be obtained from them, the issue of lack of sampling must be dealt with. On page 12 they write "Although the bottom of the well for 3 energy minima from PCA represent the most stable overall conformation of the protein, they do not convey direct information regarding agonist stability or orientation". The reasons why not must be explained; as they should do just that if the two order parameters PC1 and PC2 captured the slowest degrees of freedom for binding and sampling was sufficient. The authors write that "For all agonists and trajectories, m3 had the least variance (was most stable), again supporting convergence by 200 ns." Again the issue of actual free energy values in the maps needs to be dealt with. The probabilities expressed as -kTln rho in kcal/mol might suggest that m2 is the most stable. Instead, the authors base stability only on variance (I guess breadth of the well?), where m3 may be more localised in the chosen PC space, despite apparently having less preference during the MD (not the lowest free energy in the maps).

The motivations and justifications for use of approximate PBSA energetics instead of atomistic MD free energies should be dealt with in the manuscript, with limitations more clearly discussed. Rather than using modern all-atom MD free energy methods for relative or absolute binding free energies, the author select clusters from their identified states and do Poisson-Boltzmann estimates (electrostatic, vdW, surface area, vibrational entropy). I do believe the following sentence does not begin to deal with the limitations in that method: "there are limitations with regard to MM-PBSA accurately predicting absolute binding free energies (Genheden & Ryde, 2015; Hou et al., 2011) that depends on parameterization of the ligand (Oostenbrink et al., 2004)." What are the assumptions and limitations in taking a continuum electrostatics (presumably with parameters for dielectric constants and their assignments to regions after discarding solvent), surface area (with its assumptions and limitations) and of course assuming vibration of a normal mode can capture entropy. On page 30, regarding their vibrational entropy estimate, they write that the "entropy term provides insights into the disorder within the system, as well as how this disorder changes during the binding process". It is important that the extent of disorder captured by the vibrational estimate be discussed, as it is not obvious that it has captured entropy involving multiple minima on the system's true 3N-dimensional energy surface, and especially the contribution from solvent disorder in bound Vs dissociated states.

As discussed above, errors in the free energy estimates need to be more faithfully represented, as fractional errors are not meaningful. On page 21 the authors write "The match improved when free energy ratios rather than absolute values were compared." But a ratio of free energies is not a typical or expected measure of error in delta G. They also write "For ACh and CCh, there is good agreement between.Gm1 and GLA and between.Gm3 and GHA. For these agonists, in silico values overestimated experimental ones only by ~8% and ~25%. The agreement was not as good for the other 2 agonists, as calculated values overestimated experimental ones by ~45%(Ebt) and ~130% (Ebt). However, the fractional overestimation was approximately the same for GLA and GHA." See above comment on how this may misrepresent the error. On page 21 they write, in relation to their large fractional errors, that they "do not know the origin of this factor but speculate that it could be caused by errors in ligand parameterization". But the estimates from the PBSA approach are, by design, only approximate. Both errors in parameterisation (and their likely origin) and the approximate model used, need discussion.

Reviewer #3 (Public Review):

Summary:

The authors use docking and molecular dynamics (MD) simulations to investigate transient conformations that are otherwise difficult to resolve experimentally. The docking and simulations suggest an interesting series of events whereby agonists initially bind to the low affinity site and then flip 180 degrees as the site contracts to its high affinity conformation. This work will be of interest to the ion channel community and to biophysical studies of pentameric ligand-gated channels.

Strengths:

I find the premise for the simulations to be good, starting with an antagonist bound structure as an estimate of the low affinity binding site conformation, then docking agonists into the site and using MD to allow the site to relax to a higher affinity conformation that is similar to structures in complex with agonists. The predictions are interesting and provide a view into what a transient conformation that is difficult to observe experimentally might be like.

Weaknesses:

A weakness is that the relevance of the initial docked low affinity orientations depend solely on in silco results, for which simulated vs experimental binding energies deviate substantially for two of the four ligands tested. This raises some doubt as to the validity of the simulations. I acknowledge that the calculated binding energies for two of the ligands were closer to experiment, and simulated efficiencies were a good representation of experimental measures, which gives some support to the relevance of the in silico observations. Regardless, some of the reviewers comments regarding the simulation methodology were not seriously addressed.

Reviewer #4 (Public Review):

Summary:

In their revised manuscript "Conformational dynamics of a nicotinic receptor neurotransmitter binding site," Singh and colleagues present molecular docking and dynamics simulations to explore the initial conformational changes associated with agonist binding in the muscle nicotinic acetylcholine receptor, in context with the extensive experimental literature on this system. Their central findings are of a consistently preferred pose for agonists upon initial association with a resting channel, followed by a dramatic rotation of the ligand and contraction of a critical loop over the binding site. Principal component analysis also suggests the formation of an intermediate complex, not yet captured in structural studies. Binding free energy estimates are consistent with the evolution of a higher-affinity complex following agonist binding, with a ligand efficiency notably similar to experimental values. Snapshot comparisons provide a structural rationale for these changes on the basis of pocket volume, hydration, and rearrangement of key residues at the subunit interface.

Strengths:

Docking results are clearly presented and remarkably consistent. Simulations are produced in triplicate with each of four different agonists, providing an informative basis for internal validation. They identify an intriguing transition in ligand pose, not well documented in experimental structures, and potentially applicable to mechanistic or even pharmacological modeling of this and related receptor systems. The paper seems a notable example of integrating quantitative structure-function analysis with systematic computational modeling and simulations, likely applicable to the wider journal audience.

Weaknesses:

The response to initial review is somewhat disappointing, declining in some places to implement suggested clarifications, and propagating apparent errors in at least one table (Fig 2-source data 1). Some legends (e.g. Fig 2-supplement 4, Fig 3, Fig 4) and figure shadings (e.g. Fig 2-supplement 2, Fig 6-supplement 2) remain unclear. Apparent convergence of agonist-docked simulations towards a desensitized state (l 184) is difficult to interpret in absence of comparative values with other states, systems, etc. In more general concerns, aside from the limited timescales (200 ns) that do not capture global rearrangements, it is not obvious that landscapes constructed on two principal components to identify endpoint and intermediate states (Fig 3) are highly robust or reproducible, nor whether they relate consistently to experimental structures.

Author Response

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Review):

Weaknesses:

The weaknesses are the brevity of the simulations, the concomitant lack of scope of the simulations, the lack of depth in the analysis, and the incomplete relation to other relevant work.

A 1 µs simulation of CCh (Video 1, part 2) shows that m3 (ACHA) is stable, throughout. The DG comparisons, in silico versus in vitro, indicate that 200 ns simulations are sufficient to identify LA versus HA conformational populations. Figure 6-table supplement 1 shows distances. New citations have been added.

Reviewer #2 (Public Review):

Weaknesses:

After carrying out all-atom molecular dynamics, the authors revert to a model of binding using continuum Poisson-Boltzmann, surface area, and vibrational entropy. The motivations for and limitations associated with this approximate model for the thermodynamics of binding, rather than using modern atomistic MD free energy methods (that would fully incorporate configurational sampling of the protein, ligand, and solvent) could be provided. Despite this, the authors report a correlation between their free energy estimates and those inferred from the experiment. This did, however, reveal shortcomings for two of the agonists. The authors mention their trouble getting correlation to experiment for Ebt and Ebx and refer to up to 130% errors in free energy. But this is far worse than a simple proportional error, because -24 Vs -10 kcal/mol is a massive overestimation of free energy, as would be evident if the authors were to instead express results in terms of KD values (which would have an error exceeding a billion fold). The MD analysis could be improved with better measures of convergence, as well as a more careful discussion of free energy maps as a function of identified principal components, as described below. Overall, however, the study has provided useful observations and interpretations of agonist binding that will help understand pentameric ligand-gated ion channel activation.

The objective of the calculations was to identify structural populations, not to estimate binding free energies. We knew the actual LA and HA energies (for all 4 agonists) from real-world electrophysiology experiments. We conclude that the simple PBSA method worked as a tool for identification because the calculated efficiencies match those from experiments (Figure 4B, Figure 4-Source Data 1). We discuss the mismatches in absolute G in the Results and Discussion. Methods for estimating experimental binding free energies are described in a cited, eLife companion paper. The G ratio relates to agonist efficiency.

Main points:

Regarding the choice of model, some further justification of the reduced 2 subunit ECD-only model could be given. On page 5 the authors argue that, because binding free energies are independent of energy changes outside the binding pocket, they could remove the TMD and study only an ECD subunit dimer. While the assumption of distant interactions being small seems somewhat reasonable, provided conformational changes are limited and localised, how do we know the packing of TMD onto the ECD does not alter the ability of the alpha-delta interface to rearrange during weak or strong binding? They further write that "fluctuations observed at the base of the ECD were anticipated because the TMD that offers stability here was absent.". As the TMD-ECD interface is the "gating interface" that is reshaped by agonist binding, surely the TMD-ECD interface structure must affect binding. It seems a little dangerous to completely separate the agonist binding and gating infrastructure, based on some assumption of independence. Given the model was only the alpha and delta subunits and not the pentamer with TMD, I am surprised such a model was stable without some heavy restraints. The authors state that "as a further control we carried out MD simulation of a pentamer docked with ACh and found similar structural changes at the binding pocket compared to the dimer." Is this sufficient proof of the accuracy of the simplified model? How similar was the model itself with and without agonist in terms of overall RMSD and RMSD for the subunit interface and the agonist binding site, as well as the free energy of binding to each model to compare?

The statement that distant interactions are small is not an "assumption", but rather a conclusion based on data. Mutant cycle analysis of 83 pairs shows (with a few exceptions) non-additivity of free energy change prevails only with separations <~15 A (Fig.3 in Gupta et al 2017). Regardless, the adequacy of dimers and convergence by 200 ns are supported by the calculated and experimental agonist efficiencies match (Figure 4B) and the 1 ms simulation (Video 1 part 2). Apo 200ns simulation of the ECD dimer is now added (Figure 2-figure supplement 2) and the dimer interface seems to be adequate (stable).

Although the authors repeatedly state that they have good convergence with their MD, I believe the analysis could be improved to convince us. On page 8 the authors write that the RMSD of the system converged in under 200 ns of MD. However, I note that the graph is of the entire ECD dimer, not a measure for the local binding site region. An additional RMSD of local binding site would be much more telling. You could have a structural isomerisation in the site and not even notice it in the existing graph. On page 9 the authors write that the RMSF in Figure S2 showed instability mainly in loops C and F around the pocket. Given this flexibility at the alpha-delta interface, this is why collecting those regions into one group for the calculation of RMSD convergence analysis would have been useful. They then state "the final MD configuration (with CCh) was well-aligned with the CCh-bound cryo-EM desensitized structure (7QL6)... further demonstrating that the simulation had converged." That may suggest a change occurred that is in common with the global minimum seen in cryo EM, which is good, but does not prove the MD has "converged". I would also rename Figure S3 accordingly.

The description is now changed to “aligns well” with desensitized structure (7QL6.PDB)”. RMSD of not just the binding pocket but the whole ECD dimer is well aligned with first apo (m1) and with desensitized state (m3).

The authors draw conclusions about the dominant states and pathways from their PCA component free energy projections that need clarification. It is important first to show data to demonstrate that the two PCA components chosen were dominant and accounted for most of the variance. Then when mapping free energy as a function of those two PCA components, to prove that those maps have sufficient convergence to be able to interpret them. Moreover, if the free energies themselves cannot be used to measure state stability (as seems to be the case), that the limitations are carefully explained. First, was PCA done on all MD trajectories combined to find a common PC1 & PC2, or were they done separately on each simulation? If so, how similar are they? The authors write "the first two principal components (PC-1 and PC-2) that capture the most pronounced C. displacements". How much of the total variance did these two components capture? The authors write the changes mostly concern loop C and loop F, but which data proves this? e.g. A plot of PC1 and PC2 over residue number might help.

The PCA analyses have been enriched. Figure 3-Source Data 1. shows the dominance of PC1 and PC2. Because the binding energy match was sufficient to identify affinity states, we did not explore additional PCs. Residue-wise PC1 and PC2 analysis and comparison with RMSF are in Figure 2-figure supplement 2. PC1 and PC2 both correlate with fluctuations in loops C and F. Overlap analysis in different runs is shown in Figure 3-figure supplement 1. Lower variance in a particular region of the PCA landscape indicates that the system frequently visits these states, suggesting stability (a preference for these conformations).

The authors map the -kTln rho as a free energy for each simulation as a function of PC1 & PC2. It is important to reveal how well that PC1-2 space was sampled, and how those maps converged over time. The shapes of the maps and the relative depths of the wells look very different for each agonist. If the maps were sampled well and converged, the free energies themselves would tell us the stabilities of each state. Instead, the authors do not even mention this and instead talk about "variance" being the indicator of stability, stating that m3 is most stable in all cases. While I can believe 200ns could not converge a PC1-2 map and that meaningful delta G values might not be obtained from them, the issue of lack of sampling must be dealt with. On page 12 they write "Although the bottom of the well for 3 energy minima from PCA represent the most stable overall conformation of the protein, they do not convey direct information regarding agonist stability or orientation". The reasons why not must be explained; as they should do just that if the two order parameters PC1 and PC2 captured the slowest degrees of freedom for binding and sampling was sufficient. The authors write that "For all agonists and trajectories, m3 had the least variance (was most stable), again supporting convergence by 200 ns." Again the issue of actual free energy values in the maps needs to be dealt with. The probabilities expressed as -kTln rho in kcal/mol might suggest that m2 is the most stable. Instead, the authors base stability only on variance (I guess breadth of the well?), where m3 may be more localised in the chosen PC space, despite apparently having less preference during the MD (not the lowest free energy in the maps).

The motivations and justifications for the use of approximate PBSA energetics instead of atomistic MD free energies should be dealt with in the manuscript, with limitations more clearly discussed. Rather than using modern all-atom MD free energy methods for relative or absolute binding free energies, the author selects clusters from their identified states and does Poisson-Boltzmann estimates (electrostatic, vdW, surface area, vibrational entropy). I do believe the following sentence does not begin to deal with the limitations of that method: "there are limitations with regard to MM-PBSA accurately predicting absolute binding free energies (Genheden & Ryde, 2015; Hou et al., 2011) that depends on the parameterization of the ligand (Oostenbrink et al., 2004)." What are the assumptions and limitations in taking continuum electrostatics (presumably with parameters for dielectric constants and their assignments to regions after discarding solvent), surface area (with its assumptions and limitations), and of course assuming vibration of a normal mode can capture entropy. On page 30, regarding their vibrational entropy estimate, they write that the "entropy term provides insights into the disorder within the system, as well as how this disorder changes during the binding process". It is important that the extent of disorder captured by the vibrational estimate be discussed, as it is not obvious that it has captured entropy involving multiple minima on the system's true 3N-dimensional energy surface, and especially the contribution from solvent disorder in bound Vs dissociated states.

As discussed above, errors in the free energy estimates need to be more faithfully represented, as fractional errors are not meaningful. On page 21 the authors write "The match improved when free energy ratios rather than absolute values were compared." But a ratio of free energies is not a typical or expected measure of error in delta G. They also write "For ACh and CCh, there is good agreement between.Gm1 and GLA and between.Gm3 and GHA. For these agonists, in silico values overestimated experimental ones only by ~8% and ~25%. The agreement was not as good for the other 2 agonists, as calculated values overestimated experimental ones by ~45%(Ebt) and ~130% (Ebt). However, the fractional overestimation was approximately the same for GLA and GHA." See the above comment on how this may misrepresent the error. On page 21 they write, in relation to their large fractional errors, that they "do not know the origin of this factor but speculate that it could be caused by errors in ligand parameterization". However the estimates from the PBSA approach are, by design, only approximate. Both errors in parameterisation (and their likely origin) and the approximate model used, need discussion.

Again, the goal of calculating binding free energy was to identify structural correspondence to LA and HA and not to obtain absolute binding free energy values. Along with the least variance (distribution) for the principle component for m3, it also had the highest binding free energy. An association of m1 to LA and m3 to HA was done after comparing them to experimental values (efficiencies). This comparison not only validates our approach but also underscores the utility of PBSA in supplementing MD and PCA analyses with broader energetics perspectives.

Reviewer #3 (Public Review):

Weaknesses:

Although the match in simulated vs experimental energies for two ligands was very good, the calculated energies for two other ligands were significantly different than the experiment. It is unclear to what extent the choice of method for the energy calculations influenced the results. See above.

A control simulation, such as for an apo site, is lacking. Figure 2-figure supplement 2. shows the results of 200 ns MD simulations of the apo structure (n=2).

Reviewer #4 (Public Review):

Weaknesses:

Timescales (200 ns) do not capture global rearrangements of the extracellular domain, let alone gating transitions of the channel pore, though this work may provide a launching point for more extended simulations. A more general concern is the reproducibility of the simulations, and how representative states are defined. It is not clear whether replicates were included in principal component analysis or subsequent binding energy calculations, nor how simulation intervals were associated with specific states.

We are interested eventually in using MD to study the full isomerization, but these investigations are for the future and likely will involve full length pentamers and longer timescales. However, in response to this query we have in the Discussion raised this issue and offer speculations. See above, PCA has be compared between replicates (Figure 3-figure supplement 1).

Structural analysis largely focuses on snapshots, with limited direct evidence of consistency across replicates or clusters. Figure legends and tables could be clarified.

Snapshots and distance measurements (Figure 6-table supplement 1) were extracted from m1, m2 and m3 plateau regions of trajectories. Incorporated in the legend.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

This study gives interesting insights into the possible dynamics of ligand binding in ACh receptors and establishes some prerequisites for necessary and urgent further work. The broad interest in this receptor class means this work will have some reach.

Suggestions:

(1) I found the citation of relevant literature to be rather limited. In the following paper, the agonist glutamate was shown to bind in two different orientations, and also to convert. These are much longer simulations than what is presented here (nearly 50 µs), which allowed a richer view of conformational changes and ligand binding dynamics in the AMPA Receptor. Albert Lau has published similar work on NMDA, delta, and kainate receptors, including some of it in eLife. Perhaps the authors could draw some helpful comparisons with this work.

Yu A et al. (2018) Neurotransmitter Funneling Optimizes Glutamate Receptor Kinetics. Neuron

Likewise, the comparison to a similar piece of work on glycine receptors (not cited, https://pubs.acs.org/doi/10.1021/bi500815f) could be instructive. Several similar computational techniques were used, and interactions observed (in the simulations) between the agonist and the receptor were tested in the context of wet experiments. In the absence of an equivalent process in this paper (no findings were tested using an orthogonal approach, only compared against known results, from perhaps a narrow spectrum of papers), we have to view the major findings of the paper (docking in cis that leads to a ligand somersault) with some hesitancy.

The Gharpure 2019 paper is cited in the context of the delta subunit but this paper was about a3b4 neuronal nicotinic receptors. This could be tidied up. Also, the simulations from that paper could be used as an index of the stability of the HA state (if ligand orientation is being cited as transferrable, other observations could be too).

New citations have been added. It is difficult to generalize from Yu A and Yu R eta al, because in neither study was the ligand orientation associated with LA versus HA binding energy.

(2) "To start, we associated the agonist orientation in the hold end states as cis in AC-LA versus trans in AC-HA."

I think this a valid start, but one is left with the feeling that this is all we have and the validity of the starting state is not tested. What was really shown here? Is the docking reliable? What evidence can the authors summon for the ligand orientation that they use as a starting structure? In addition to docking energies, the match between PBSA and electrophysiology Gs and temporal sequence (m1-m2-m3) support the assignment.

Given that these simulations cover a circumscribed part of the binding process, I think the limitations should be acknowledged. Indeed the authors do mention a number of remaining open questions.

Paragraphs regarding 'catch' have been added to the Discussion.

(3) Results around line 90. Hypothetical structures and states that were determined from Markov analyses are discussed as if they are well understood and identified. Plausible though these are, I think the text should underline at least the source of such information. In these simulations, a further intermediate has been identified.

The model in Figure 1B was first published in 2012 and has been used and extended over the intervening years. In our lab, catch-and-hold is standard. We have published many papers (in top journals), plus reviews, regarding this scheme. We made presentations that are on Youtube. Here, at the end of the Introduction we now cite a new review article (Biophysical Journal, 2024). I am not sure what more we can do to raise awareness regarding catch and hold.

(4) The figures are dense and could be better organised. Figure 2 is key but has a muddled organization. The placement of the panel label (C) makes it look like the top row (0 ns) is part of (A). Panel B- what is shown in the oval inset (not labeled or in legend). Why not show more than one view, perhaps a sequence of time points? It is confusing to change the colour of the loops in (C). Please show the individual values in D.

Figure 2 has been redone.

(5) A lot is made of the aK145 salt bridge with aD200 and the distances - but I didn't see any measurements, or time course. This part is vague to the point of having no meaning ("bridge tightening").

We present a Table of distance measurements in the SI (Figure 6-table supplement 1).

Reviewer #2 (Recommendations For The Authors):

All main comments have been given in the above review. There are a few other minor comments below.

The 4 agonists examined were acetylcholine (ACh), carbamylcholine (CCh), epibatidine (Ebt), and epiboxidine (Ebx). Could the choices be motivated for the reader?

New in Methods: the agonists are about the same size yet represent different efficiency classes (citation to companion eLife paper). One of our (unmet) objectives was to understand the structural correlates of agonist efficiency.

The authors write that state structures generated in the MD simulation were identified by aligning free energy values with those from experiments. It would be good to explain to the reader, in the introduction, how LA and HA free energies were extracted from experiments, rather than relying on them to read older papers.

In the Introduction, we say that to get G, just measure an equilibrium constant and take the log. We think it is excessive to explain in detail in this paper how to measure the equilibrium binding constants (several methods suffice). However, we have added in Methods our basic approach: measure KLA and L2 by using electrophysiology, and compute KHA from the thermodynamic cycle using L0. We think this paper is best understood in the context of its companion, also in eLife.

In all equilibrium equations of the type A to B (e.g. on page 5), rather than using "=" signs it would be much better to use equilibrium reversible arrow symbols.

It is incorporated.

Reviewer #3 (Recommendations For The Authors):

(1) Although the match in simulated vs experimental energies for two ligands was very good, the calculated energies for Ebt and Ebx were significantly different than the experiment. Are there any alternative methods for calculating binding energies from the MD simulations that could be readily compared to?

See above. We did not use more sophisticated energy calculations because we already knew the answers. Our objective was to identify states, not to calculate energies.

(2) It would be nice to see control simulations of an apo site to ensure that the conformational changes during the MD are due to the ligands and not an artifact of the way the system is set up. I am primarily asking about this as the simulation of the isolated ECDs for the binding site interface seems like it may be unhappy without the neighboring domains that would normally surround it. On that note, was the protein constrained in any way during the MD?

Apo simulation results are presented in Figure 2-figure supplement 2. The dimer interface seems to be adequate (stable).

(3) Figure 4A-B: Should the colors for m1 and m3 be reversed?

Colors have been changed and a bar chart has been added.

Reviewer #4 (Recommendations For The Authors):

(1) Although simulations are commendably run in triplicate, it is difficult in some places to discern their consistency.

(1a) Table S1 provides important quantification of deviations in different replicates and with different agonists. Please confirm that the reported values are accurate. All values reported for the epibatidine system are identical to those reported for carbamylcholine, which seems statistically improbable. Similarly, runs 1 and 3 with epiboxidine seem identical to one another, and runs 1 and 2 with acetylcholine are nearly the same.

Figure 2-Source Data 1 has been corrected.

(1b) In reference to Figure S3, the authors comment that the simulated system (one replicate with carbamylcholine) converges within 0.5 Å RMSD of a desensitized experimental structure. This seems amazing; please specify over what atoms this deviation was calculated and with reference to what alignment. It would be interesting to know the reproducibility of this remarkable convergence in additional replicates or with other ligands; for example, Figure 5 indicates that loop C transitions to a lesser extent in the context of epibatidine than other agonists.

The comparison was for the entire dimer ECD; 0.5 Å is the result. It may be worthwhile to pursue this remarkable convergence, but not in this paper. Here, we are concerned with identifying ACLA and ACHA. Similarity between ACHA and AD structures is for a different study.

(1c) For principal-component and subsequent analyses, it appears that only one trajectory was considered for each system. Please clarify whether this is the case; if so, a rationale for the selection would be helpful, and some indication of how reproducible other replicates are expected to be.

We have added new PCA results (Results, Figure 3-figure supplement 1) that show comparable principal components in other replicates.

(2) Figure 3 shows free energy landscapes defined by principal components of fluctuation in Cα positions.

(2a) Do experimental structures (e.g. PDB IDs 6UWZ, 7QL6u) project onto any of these landscapes in informative ways?

6UWZ.pdb matches well with the apo (7QKO.pdb), comparable to m1, and 7QL6.pdb with the m3.

(2b) Please indicate the meaning of colored regions in the righthand panels.

The color panels in the top left panel indicate the colored regions in the righthand panel also, which is indicative of direction and magnitude of changes with PC1 and PC2.

(2c) Please also check the legend; do the porcupine plots really "indicate the direction and magnitude of changes between PC1 and PC2," or rather between negative and positive values of each principal component?

It indicates the direction and magnitude of changes with PC1 and PC2.

(3) It would be helpful to clarify how trajectory segments were assigned to specific minima, particularly m2 and m3.

(3a) Please verify the timeframes associated with the m2 minima, reported as "20-50 ns [with acetylcholine], 50-60 ns [with carbamylcholine], 60-100 ns [with epibatidine, and] 100-120 ns [with epiboxidine]." It seems improbable that these intervals would interleave so precisely in independent systems. Furthermore, the intervals associated with acetylcholine and epiboxidine do not appear to correspond to the m2 regions indicated in Figure S8.

Times are given in Figure 4-Source Data 1 and Figure 3-figure supplement 2. The m2 classification is based on loop displacement as well as agonist orientation. For all agonists, the selection was strictly from PCA and cluster analysis.

(3b) The text (and legend to Figure 3) indicate that 180+ ns of each trajectory was assigned to m3, which seems surprisingly consistent. However, Figure S5 indicates this minimum is more variable, appearing at 160 ns with acetylcholine but at 186 ns with carbamylcholine. Please clarify.

see above: the selection was from PCA and cluster analysis. Times are in Figure 3-figure supplement 2 and also in Figure 4-Source Data 1 (none in Fig. 3 legend).

(3c) Figures 5, 6, S6, and S7 illustrate structural features of free-energy minima in each ligand system. Please clarify what is shown, e.g. a representative snapshot, centroid, or average structure from a particular prominent cluster associated with a given minimum.

They are all representative snapshots (now in Methods). Snapshots and distance measurements (Figure 6-table supplement 1) were extracted from m1, m2 and m3 plateau regions of trajectories.

(4) Figure S4 helpfully shows the behavior of a pentameric control system; however, some elements are unclear.

(4a) The 2.5-6.5 Å jump in RMSD at ~40 ns seems abrupt; can it be clarified whether this corresponds to a transition to either m2 or m3 poses, or to another feature of e.g. alignment?

Figure 2-figure supplement 4 left bottom is just the ligand. The jump is the flip, m1 to m2.

(4b) It seems difficult to reconcile the apparently bimodal distribution of states with the proposed 3-state model. Into which RMSD peak would the m2 intermediate fall?

The simulations are only to 100 ns, where we found a complete flip of the agonist represented in the histograms. This confirmed that dimer showed similar pattern as the pentamer. In depth analysis was only done only on dimers.

(4c) The top panel is labeled "Com" with a graphical legend indicating "ACh." Does this indicate the ligand or, as described in the text legend, "the pentamer" (i.e. the receptor)? For both panels, please verify whether they are calculated on the basis of center-of-mass, heavy atoms, Cα, etc.

"Com" (for complex) has been changed to system (protein+ligand).

(5) Minor concerns:

(5a) In Figures 1 and S3, correct the PDB references (6UWX and 7QL7 are not nAChRs).

They are now corrected.

(5b) In Figure 4, do all panels represent mean {plus minus} standard deviation calculated across all cluster-frames reported in Table 1?

Yes.

Also check the graphical legend in panel A: presumably the red bars correspond to m1/LA, and the blue to m3/HA?

Corrected

(5c) In the legend to Figure S1, please clarify that panel B is reproduced from Indurthi & Auerbach 2023.

This figure has been deleted.

(5d) As indicated in Figure S2, it seems surprising that the RMSF is so apparently low at the periphery, where the subunits should contact neighbors in the extracellular domain; how might the authors account for this? Specify whether these results apply to all replicates of each system.

The redness in the periphery for all four systems indicates the magnitude of fluctuation. As we focus on the orthosteric site, we highlight the loops around the agonist binding pocket and kept other regions 75% transparent. We now include Apo simulations and the dimer appears to be stable even without an agonist present.

(5e) Within each minimum in Figure S5, three "prominent" clusters appear to be colored (by heteroatom) with carbons in cyan, pink, and yellow respectively. If this is correct, note these colors in the text legend.

Colors have been added to the legend.

(5f) In Figure S6, note in the legend that key receptor sidechains are shown as spheres, with the ligand as balls-and-sticks, and that ligand conformations in both low- and high-affinity complexes are shown in both receptor states for comparison.

This is now added in the legend.

(5g) The legend to Figure S6 also notes "The agonists are as in Fig S4," but that figure contains a single replicate of a different system; please check this reference.

This has been updated to Figure 5.

(5h) In Figure S8, the colors in the epibatidine system appear different from the others.

The colors are the same for m1, m2 and m3 in all systems including epibatidine.

(5i) In Table 1, does "n clusters" indicate the number of simulation frames included in the three prominent clusters chosen for MM-PBSA analysis? Perhaps "n frames" would be more clear.

It was a good suggestion. It has now been changed to ‘n frames’

(5j) Pg 24-ln 453 presumably should read "...that separate it from m1 and m3..."

This sentence is now changed in the discussion.