Consolidated peer review report (26 September 2024)

GENERAL ASSESSMENT

In this article, Kay refutes a major claim made by Watson et al., 2023. In the original publication, Watson et al. argue that macromolecular condensation acts as a cellular buffering mechanism to compensate for the effects of osmotic shock. In particular, they claim that, when water is drawn into or out of the cell due to hypo- or hyper-osmotic shock, respectively, macromolecular condensates rapidly capture (during hypo-osmotic shock) or release (during hyper-osmotic shock) free water to maintain a constant water potential (presumably in addition to a constant solute concentration and osmolality) within the cell. While Watson et al. find that macromolecular condensation in cells is responsive to osmotic shock, they do not measure intracellular water potential, osmolality, or macromolecular density in intact cells, and therefore do not directly demonstrate that biocondensation buffers any of these properties in living cells. In response, Kay argues that, while such a water buffer could temporarily maintain an osmolality differential across the membrane, this osmolality differential will necessarily drive water across the membrane until the osmolality within the cell equals the osmolality outside of the cell. Therefore, the steady-state behaviour is expected to be identical with and without the water buffer. Using the well-established pump-leak model for osmotic water transport, Kay further shows that the timescale at which a water buffer can maintain even a 10% osmolality differential across the membrane is at most a minute for a typical animal cell.

Overall, Kay 2024 provides a compelling rebuttal to a strong claim made by Watson et al. However, there is an opportunity for Kay to acknowledge nuanced situations where such a water buffering mechanism as that posited by Watson may be useful to cells. It’s also unclear if Kay has described a major inconsistency with Watson et al., particularly since the water release rate from condensates is not well quantified.

RECOMMENDATIONS

Essential revisions:

1. The author could acknowledge nuanced situations in which the water buffering mechanism described by Watson et al. may be useful to cells. For example, by slowing the rate of change of intracellular osmolarity due to osmotic shock and thus giving the cell time for more active feedback mechanisms to engage, or in buffering rapid fluctuations in extracellular osmolality
2. The flux of water across lipid membranes depends on the pressure difference across the membrane. The author simulated the situation with a 30 mOsm (~75 kPa) osmotic pressure difference. Considering that physiologically relevant pressure fluctuations can be much lower (a few kPa), is it possible that a water buffer would be more effective when there are small pressure differences across the cell membrane? The author should discuss this.
3. The author should cite the work from which they obtained the water buffer release rate.
4. It would be helpful to measure the dynamics of intracellular volume concurrently with biocondensate formation under cells exposed to osmotic shock (ideally under experimental conditions where cells either do or do not form condensates). If Watson et al.’s hypothesis is correct, the volume should not change (this seems unlikely). If your hypothesis is correct that buffering could only ever be temporary, one could then experimentally determine the buffering timescale by measuring the stall time between the shock and when the volume begins to change. The stall should also disappear in conditions where condensate formation is inhibited.
5. There are two inaccuracies in the discussion of membrane tension caused by osmotic pressure that would benefit from being corrected. First, when using Laplace’s Law to calculate membrane tension induced by 30 mOsm pressure, the author used a cell radius of 10 um and calculated a large (180 mN/m) membrane tension. This is significantly overestimated because the cell membrane can form local deformations via attachment to the cytoskeleton. These local deformations are typically around 10 - 100 nm, thus reducing the calculated membrane tension by 2-3 orders of magnitude, below the lysis tension of the membrane (1 - 10 mN/m). Second, the author is correct that measured resting membrane tension is low (< 0.3 mN/m). However, recent evidence suggests that tension on the cell membrane can locally or transiently reach much higher levels (to > 1mN/m). This is supported by activation of mechanosensitive ion channels such as Piezo1, which require an activation membrane tension ~ 1mN/m.
6. The discussion on non-equilibrium states is not very clear. Is the author suggesting that a water buffer can work more efficiently in an equilibrium system such as a giant vesicle?
7. Because the pump-leak model is generic, some contextual discussion of condensates would be helpful. For example, the dynamic formation of hydrogen bonds, van der Waals interactions, and possible charges resulting from hyperosmotic or low osmotic conditions that may indirectly participate in the hypothesis.
8. Has the author considered whether the thermodynamic driving forces associated with phase separation and condensate formation might affect the ability of condensates to buffer intracellular osmolality?

Optional suggestions:

1. The language of the article focuses on the role of membrane permeability, which is of course key. However, it might be helpful to explicitly state that an osmolality differential will always drive water across the membrane, so even if a water buffer could temporarily maintain such an osmolality differential, water will continue to flow across the membrane until the buffer is saturated and this differential is equalized.

REVIEWING TEAM

Reviewed by:

Rikki Garner, Postdoctoral Research Fellow, Harvard Medical School, USA: physics, biophysics, and physical/quantitative cell biology.

Tripta Bhatia, Assistant Professor, Indian Institute of Science Education and Research Mohali, India: soft matter, biological physics, membrane biophysics

Zheng Shi, Assistant Professor, Rutgers University-New Brunswick, USA: mechanics of biomolecular assemblies

Curated by:

Syma Khalid, Professor, University of Oxford, UK

(This consolidated report is a result of peer review conducted by Biophysics Colab on version 1 of this preprint. Comments concerning minor and presentational issues have been omitted for brevity.)

Consolidated peer review report (24 May 2024)

GENERAL ASSESSMENT

The preprint by Vats et al. (2023) introduces a methodology of applying slow feature analysis (SFA) to AlphaFold ensembles, with the goal of identifying collective variables for subsequent MD simulations.

The study aims to leverage AlphaFold's predictive capabilities to enhance understanding of protein dynamics and rare events, such as cryptic pocket opening, protein-ligand binding/unbinding, and allosteric modulation. By integrating AlphaFold predictions with molecular dynamics (MD) simulations and slow feature analysis (SFA), the objective is to develop a comprehensive framework for efficiently sampling and analyzing these critical molecular events in ways that might not be sampled by classical simulations or using traditional collective variables alone.

Key findings are that AlphaFold-generated structural ensembles provide useful initial conformations that capture essential conformational heterogeneity. The study demonstrates the utility of AlphaFold in seeding MD simulations to capture rare events, such as the flipping of key residues necessary for cryptic pocket opening in plasmepsin II. In the RIPK2 test case, conformational alterations in the activation loop and DFG moiety elucidate their roles in protein function and interactions relevant to inflammatory diseases. Integration of SFA with metadynamics allows for the efficient sampling of rare events within a shorter simulation time compared to traditional methods, thereby accelerating the exploration of protein dynamics. Generally, their approach works for sampling relevant conformational changes in both side chains and backbones for at least two test cases.

Strengths of this work include the well written description of the SFA method, and demonstration of success in two distinct cases. Integrating AlphaFold with computational methods like SFA and metadynamics is in principle a powerful approach to studying protein dynamics and functional mechanisms, with potential applications in drug discovery and disease understanding. This study showcases the synergy between AI-based protein structure prediction and computational biology, facilitating more comprehensive and efficient exploration of protein dynamics and interactions.

Weaknesses include a lack of clarity as to what input data are required to run the method, what criteria were used to measure success, and what specifically is learned by the application of SFA, as well as some missing figure captions and citations. A general concern about applicability is the use of vanilla AlphaFold predictions as starting points for molecular dynamics, for example given the tendency of the AlphaFold inference system to bias towards states with more contacts.

RECOMMENDATIONS

The manuscript in its current state is convincing in presenting the method, but could benefit from reorganization and streamlining to more directly expose the relevant results to the reader.

Essential revisions:

1. The manuscript is not clear in defining what data are required to run this method. The initial modeling is done with AlphaFold, which requires only an input sequence. However, the pipelines for the two main test cases are quite different, with two 40-ns simulations for each of the 80 AlphaFold models of plasmepsin-II, but ten 20-ns simulations for each of 32 AlphaFold models of RIPK2; no explanation is given for these different parameterizations. More importantly, for plasmepsin-II the metadynamics simulations were executed on PDB structures instead of AlphaFold models, implying that such structures are in fact necessary. It is not clear what the starting structure was used for metadynamics simulations of RIPK2. The authors should clearly state whether they believe experimental structures as metadynamics inputs are necessary for this method to work, as it is an important consideration for prospective users.
2. Confidence in AlphaFold-generated models should be analyzed, or at least discussed. The underlying assumption regarding the presence of conformational diversity in the generated ensemble is speculative at best. The proposed method could be tested in protein systems with known conformational states as references to validate sampling; methods like AFcluster1 or SPEACH_AF2 could enhance diversity.
3. There are relatively few details about what specifically is learned by the application of SFA. Although the details of the approach for the given systems are clearly described in Methods, there is little description of its applicability to other fields. In Results, figures S3A and S8 aim to explain the learned features for plasmepsin-II and RIPK2 respectively, but it is not clear what these features are, or what exactly is communicated. The x-axes are particularly confusing, as they seem to indicate a sequential index of features that do not correspond to amino acids (for example, the text refers to Phe165 in RIPK2, but the x-axes in S8 end around 150). Although machine-learning-derived features are often difficult to explain, it would help to clarify the x-axis titles, and add qualitative descriptions to the text and/or captions. There are also few examples for how metadynamics with SFA-picked CVs compares to traditional metadynamics with hand-picked CVs. Figures 8E/F, S12, and S13 compare how this method captures transitions of RIPK2 between the two states of interest, while unbiased simulations do not; but otherwise, the authors rely on prior publications to illustrate advantages of their approach in uncovering cryptic pockets.

Optional suggestions:

1. The tests being carried out to evaluate success should be clarified. In the case of plasmepsin-II, success was evaluated on the basis of chi-angle rotations of Trp41 and Tyr77; for RIPK2, the relevant residues were Phe165 and Trp170. However, these residues are only introduced (briefly) in Methods, then explained in somewhat more detail in Results. It would be helpful to add at least one or two sentences about these residues in the Introduction.
2. The number of samples is an important factor in determining the extent of conformational diversity in the ensemble generated by AlphaFold. Optimizing this for downstream metadynamics-SFA should expedite convergence, as it is highly dependent on initial states.
3. In the simulations field, it is common to use time-lagged component analysis (TICA) to describe slow modes of motion. Could the authors compare their method with this previously established approach?
4. Before training SFA, the authors performed parallel MD simulations starting from the AlphaFold-generated seeds. It would be nice to see what conformational space is covered during the initial unbiased MD simulations, to see what information is gained from these relative to the static starting positions of the AlphaFold models. Are these simulations connected in the space that is used to train SFA? If not, how could this affect the analysis?
5. The description of RIPK2 on p. 14, particularly its biological relevance, seems out of place in Results. Consider moving some of this content to Introduction and/or Discussion.

REVIEWING TEAM

Reviewed by:

Diego del Alamo, Investigator, GSK, Switzerland: protein design, deep learning

Nandan Haloi, Postdoctoral Fellow, KTH Royal Institute of Technology, Sweden: molecular dynamics simulations, enhanced sampling, Markov state modeling

Yogesh Kalakoti, Postdoctoral Fellow, Linköping University, Sweden: computational biology, large language models, structural bioinformatics

Curated by:

Rebecca J. Howard, Senior Researcher, Stockholm University, Sweden

(This consolidated report is a result of peer review conducted by Biophysics Colab on version 2 of this preprint. Comments concerning minor and presentational issues have been omitted for brevity.)

Consolidated peer review report (6 October 2023)

GENERAL ASESSMENT

This article will be of broad interest to readers in the field of protein folding, amyloid biogenesis and biotechnology. It provides new structural information on the pre-amyloid forms of a functional amyloid, curli, enabling new insight into nucleation mechanism of this protein. The authors used sequence analysis and construct design to generate a slow folding variant of the CsgA kernel, designated “slowgo”, which enabled detailed analysis of the folding kinetics using NMR. In addition they used native Mass Spectrometry and cryo-EM to identify the smallest folded CsgA species, and discovered it was a β-solenoid dimer. The authors propose a new model for curli formation, which proceeds via an initial slow folding step that places constraints on the rate of fibril formation in the cytoplasm, before efficient extracellular polymerization occurs outside the cell. Together, these results explain how curli is able to transit the cytoplasm without forming harmful aggregates and provide new insights into designer functional amyloids that will be useful in biotechnology and synthetic biology.

All three reviewers consider the work to be well-written, original, of high quality in terms of experimental data, and the experiments well-designed and controlled. The conclusions drawn from the work rely heavily on the development of the “slowgo” variant of the CsgA protein. The main suggestions to strengthen the conclusions are based on further validation of the assumptions concerning the behaviour of this species. Our recommendations for additional experiments are detailed below and aim to strengthen the conclusions made concerning this variant.

RECOMMENDATIONS

Essential revisions:

1. The authors mention that CsgA and its “slowgo” variant remain monomeric in a molten globule state until they transition into a dimeric folded state. The authors use NMR, DLS, and radius of gyration analysis to support this claim. Given that the monomeric state seems to be stable enough, especially for the “slowgo” variant, it would be very helpful to confirm this via a native gel. If these claims are true, CsgA should be clearly observed in the monomeric state during the first minutes of the reaction for WT, and up to 40 hours for the slowgo mutant, as indicated by the authors. In addition, the authors could run aliquots from the aggregation reaction taken at different times in denaturing gels to probe the SDS-resistance and stability of the oligomeric and amyloid species. We think this is a direct and simple way of testing the monomeric state of CsgA, which is central in the model proposed by the authors.
2. The authors reference the well-established sigmoidal ThT-kinetics to underpin their hypothesis that an initial slow folding step places constraints on the rate of fibril formation. However, could the initial part of the sigmoidal curve (known as lag phase before elongation) be due to other processes such as low dimerization or binding affinity of the monomers? We think it would be helpful to discuss these other possibilities or provide additional experimental evidence that these are not involved in the rate of nucleation and rate of fibril formation.
3. Additional analysis of the NMR data in the context of the “slowgo” construct substitutions would provide additional insight into the impact these mutations have on the folding kinetics. For example, all four substitutions detailed in the study introduce an alanine into the protein, which has a high helical propensity. Two are made in regions that promote helicity, whereas the other two variants do not promote helicity. However, it is not indicated whether these are β-solenoid strand positions or whether they are inward-facing or outward-facing. Additional clarification would help the reader understand the context of these mutations within the structure.
4. Similarly, additional analyses of where the regions with helical propensity lie within the context of the extended/strand portions of the folded β-solenoid secondary structure would help put the NMR data into clearer context. The regions predicted to have helical propensity are short, almost all less than a turn, and none have significant propensities above 50%; at the same time, non-extended conformations are needed for the solenoid to fold back on itself and short stretches with helical backbone angles are not necessarily disruptive. One suggestion is that Figure 5 could indicate whether each position in the repeat is extended or not in the β-solenoid structure and, correspondingly, whether the Pβ is calculated over just the extended region.
5. Could the authors undertake a continuous acquisition nMS experiment where they can observe the oligomerization progressing as a function of time? This would enable them to quantitively show the changes in oligomerization dynamics. If this gets too difficult to perform, the authors can expand their Supporting Figure 6 and have more granular time point data and plot the same for each oligomeric species observed for each protein-forms. This would provide strong evidence for the folding mechanism proposed.

Optional suggestions:

1. From Supporting Figure 6 data on time-resolved nMS it is concluded that the dimer must be on-pathway. However, depending on the rate equations, is it possible that the dimer pool is reversibly formed off-pathway but then depleted once most of the protein is incorporated into amyloids? Based on all the data together, the conclusion adopted by the authors seems likely, but perhaps the wording could be softened to indicate other possibilities do exist.
2. Figure 6 should be improved for clarity. Some states are unclear due to the choice of color and the design of cartoons.
3. Indicate temperature for the NMR studies in Fig. 1a. The rate of signal loss is faster than that seen by ThT fluorescence in Supporting Figure 1, which would suggest the possibility of a longer-lived intermediate. Is the NMR done at 25C?
4. The flow of the introduction would benefit from separation into more paragraphs. It would also benefit from a clearer description of the differences between the NCC mechanism and the one CsgA is thought to follow; this is an essential piece of background and strongly motivates the work here, but confusion arises from the use of the terms nucleation and oligomerisation within the two contexts.
5. Considering the proportion of residues exhibiting helicity and the magnitude it would be better to show much less helix in the schematic of Figure 6.
6. Considering the importance of Figure 2, it should be indicated how the chemical shifts were referenced, which can have significant effects on secondary shift analysis. It is indicated that TALOS was used for secondary structure predictions, but the data looks more like what one obtains from delta2d? If it was TALOS, the version should be indicated.

REVIEWING TEAM

Reviewed by:

Piere Rodriguez Aliaga, Postdoctoral Scholar, Stanford University, USA: protein biophysics, IDPs, protein misfolding and aggregation, chaperones, single molecule biophysics

Kallol Gupta, Assistant Professor, Yale University, USA: native mass spectrometry, protein folding

Jason Schnell, Associate Professor, University of Oxford, UK: protein solution NMR; protein folding

Curated by:

Simon Newstead, Professor, University of Oxford, UK

(This consolidated report is a result of peer review conducted by Biophysics Colab on version 1 of this preprint. Comments concerning minor and presentational issues have been omitted for brevity.)

Evaluation statement (17 January 2024)

The study by Bassetto Jr. et al. presents an elegant and pioneering technique to rapidly manipulate membrane temperature by up to 10 ºC in less than 1.5 ms, thereby enabling high temporal resolution of the temperature dependence of ion channel currents. The approach combines the cut-open oocyte voltage clamp technique with laser illumination to heat the sub-membrane melanosome layer. Temperature is quantified from observed changes in membrane capacitance. Recordings of Kir1.1, TRPM8, and TRPV1 channels are used to validate the effectiveness of the technique. A limitation is that, in its current form, the technique can be used only on melanosome-containing Xenopus oocyte membranes.

Biophysics Colab recommends this study to scientists working on the temperature dependence of ion channels and other membrane proteins.

Biophysics Colab has evaluated this study as one that meets the following criteria: - Rigorous methodology - Transparent reporting - Appropriate interpretation

(This evaluation refers to the version of record for this work, which is linked to and has been revised from the original preprint following peer review.)

Evaluation statement (8 March 2024)

Seljeset et al. investigate the mechanism by which NMDA receptors are activated by co-agonists glutamate and glycine. By mutating residue Asp732 in the glycine-binding site, they generate receptors activated by glutamate, and not glycine, but inhibited by glycine antagonists. Conventional and unnatural amino acid mutagenesis reveals that Asp732 interacts with nearby residues to influence channel gating as well as ligand binding. Furthermore, a homomeric receptor from Trichoplax adhaerens, which has a tyrosine in the homologous position, displays constitutive activity that becomes glycine-dependent when the tyrosine is mutated to aspartate. The study is valuable because it reveals the importance of position 732 for controlling ligand potency and channel activity in glutamate receptors, which should lead to a better understanding of how these receptors are primed for channel opening.

Biophysics Colab recommends this study to scientists interested in the structure and function of glutamate receptors

Biophysics Colab has evaluated this study as one that meets the following criteria:

• Rigorous methodology
• Transparent reporting
• Appropriate interpretation

(This evaluation refers to version 2 of this preprint, which has been revised in response to peer review of version 1.)

Evaluation statement (17 January 2024; revised 31 January 2024)

Feng and colleagues investigate the molecular basis of lipid scrambling in a fungal member of the TMEM16 family of Ca²⁺-dependent lipid scramblases. These proteins possess a groove in their 3D structure that has been implicated in lipid scrambling, which the authors investigate in the absence and presence of Ca²⁺ using a combination of cryo-EM structure determination, mutagenesis and functional assays. Their closed-groove structure reveals a continuous file of lipid molecules around the catalytic groove region, providing a structural basis for lipid interaction with the protein. Additionally, the authors capture three novel states of TMEM16, completing the picture of conformational transitions that this protein undergoes. Strikingly, the authors show that both structure and distribution of the protein’s conformations depend on lipid composition and nanodisc scaffold protein.

Biophysics Colab considers this to be exceptional work and recommends it to scientists interested in plasma membrane lipid homeostasis and cryoEM.

(This evaluation by Biophysics Colab refers to version 2 of this preprint, which has been revised in response to peer review of version 1.)

Authors’ response (3 January 2024)

GENERAL ASSESSMENT

The TMEM16 protein family is composed of ten members in mammals, and fewer in lower eukaryotes. Members within this protein family play remarkably different roles: some serve as Ca²⁺-activated ion channels, others work as lipid scramblases in a Ca²⁺-dependent manner, and some combine the two functions. The molecular determinants responsible for lipid transport in TMEM16 scramblases are not fully defined. The current view of lipid scrambling is that, in presence of Ca²⁺, TMEM16 scramblases change their conformation to expose a hydrophilic ‘groove’ to the membrane. This destabilizes the lipid bilayer, enabling translocation of lipids (e.g. phosphatidylserine) from the inner to outer leaflet of the membrane. However, recent evidence suggests that scrambling can occur even when the hydrophilic groove is closed.

The new study by Feng and colleagues aims to investigate the molecular basis of closed-groove scrambling using the fungal scramblase, nhTMEM16. This protein was previously reported to maintain closed groove conformations even in the presence of Ca²⁺. The authors resolved a series of WT nhTMEM16 structures in two different nanodisc scaffolds, as well as several mutants with impaired scrambling. Strikingly, the conformational landscape of nhTMEM16 was found to rely on the lipid composition and scaffold used: the smaller E3D1 scaffold favored closed groove states and the larger 2N2 scaffold permitted intermediate and open-groove conformations. A high-resolution closed-groove structure obtained in E3D1 allowed the identification of a continuous file of lipid molecules around the catalytic groove region, providing a structural basis for lipid interaction with the closed groove. This complements prior work from this group involving a closely-related homolog, afTMEM16, in which the authors were able to visualize lipid molecules around the open groove. Furthermore, the authors succeeded in capturing three novel states of nhTMEM16 (Ca²⁺-free closed, Ca²⁺-bound intermediate-open and Ca²⁺-bound wider open states), completing the picture of conformational transitions that this protein undergoes upon activation.

Mutation of key residues interacting with outer leaflet lipids selectively impaired scrambling in the absence of Ca²⁺. Residues involved in groove opening (E313-R432) were also identified and a mutation at this site (R432A) locked the nhTMEM16 scramblase in a closed-groove conformation, providing new insights into residues critical for groove opening. Furthermore, the authors tested the activity of nhTMEM16 mutants in several lipid compositions and reported striking differences, clarifying discrepancies from the authors’ prior work on nhTMEM16 using different lipid compositions and consolidating some of the observations from other TMEM16 homologs. It is noteworthy that the authors probed the effect of nanodisc size and lipid composition on nhTMEM16 conformation, providing thought-provoking insights for the membrane protein field. This approach is particularly valuable for closed-groove mutant structures, to ensure that the observed conformation is not dictated by scaffold size.

Overall, this is a piece of carefully executed experimental work. The results are interpreted carefully in the context of the published literature, and the work provides important insight into plasma membrane lipid homeostasis. While the study does not have technical weaknesses, it could be improved in its presentation in order to make it more accessible to readers who are not experts in the TMEM16 field.

We wish to thank the Colab editor and reviewers for their insightful comments, helpful suggestions, and appreciation of our work. We have extensively revised our manuscript to address their comments and suggestions. Below is a detailed point-by-point response to their suggestions.

RECOMMENDATIONS

Essential revisions:

1. For readers not familiar with the field, some technical details might need to be explained in greater detail. For example:

- In the section “Residues coordinating outer leaflet lipids are important in closed groove scrambling”, please indicate the method of measuring scrambling (liposome-based activity assay etc.) and refer to some of your prior work where the method is described for readers not familiar with the TMEM16 field. Additionally, it needs to be stated clearly what is considered a significant change in scrambling, as liposome assays are usually quite variable.

We thank the reviewers for this suggestion. We edited the text to indicate the use of the well-established in vitro assay and added the relevant references (Lines 236-238).

We illustrate the reproducibility of the experimental results by reporting in the bar charts the mean ± St. Dev of the scrambling rate constants, and by showing the values obtained from individual experiments (red dots superimposed to the bar charts). Additionally, we evaluated the statistical significance of the reported changes using Student’s t-test with Bonferroni correction. Finally, we added text discussing the limitations of our assay in lines 318-322.

- Since prior work done by the group indicates that membrane thinning is a determinant of scrambling, and an open groove further thins the membrane to potentiate scrambling, it is not intuitive why the R432A mutant scrambles with WT-like rates in the presence of Ca²⁺. If this is due to the limitation of the assay (e.g. rate of NBD lipids bleaching), this should be stated more explicitly. Do the authors have insights from their structures regarding membrane thinning by R432A with/without Ca²⁺ and how that compares to WT protein?

We thank the reviewers for raising this important point. In the presence of Ca2+ the fluorescence decay of N-NBD-PE in nhTMEM16 vesicles occurs with kinetics that are slightly slower than those of the chemical reduction step by dithionite. Therefore, while we can resolve two exponential components, it is possible we are underestimating the scrambling rate constants α and β. However, we note that a large slowing effect would be well resolved in our experimental conditions. In contrast, in the absence of Ca2+, which is the focus of our current analyses, scrambling is much slower than the chemical step and is well resolved. Finally, we note that the triple mutant Y327A/F330A/Y439A alone has no effect on scrambling in 0.5 mM Ca2+ but induces a ~8 fold reduction in the scrambling rate constants in 0 Ca2+. When this mutant is combined with R432A, which favors the closed groove conformation, we now see in the presence of Ca2+ the same ~8-fold reduction in the scrambling rate constants. This suggests that our assay can resolve effects even in the presence of Ca2+. This is discussed in Lines 318-322.

We only determined the structure of R432A in the presence of Ca2+, therefore we cannot evaluate how Ca2+ binding affects membrane thinning in this mutant.

- It is difficult to follow the reasoning for the R432A+Y327A/F330A/Y439A mutant phenotype. Is the assumption that Y327A/F330A/Y439A is in the open conformation with Ca²⁺, and therefore adding a mutation stabilizing the closed groove impairs scrambling in presence of Ca²⁺?

We have expanded the rationale for this experiment in lines 307-315.

- What the authors believe about the lipid pathway when the groove is open should be discussed in more detail and with reference to Alvadia et al 2019.

We thank the reviewers for this important suggestion. We now explicitly state that: “With a closed groove, thinning is less pronounced, and scrambling is slower than when the groove is open, rationalizing the Ca2+ dependence of this process (Extended Data Fig. 10d-f).” (Lines 432-434) Since the present work is focused on the mechanism of closed groove scrambling, we prefer to refrain from adding more speculations on what happens when the groove is open, especially since this topic was the focus of a paper we recently published (Falzone, Feng et al., Nat Comms, 2022).

2. A more detailed account of the physiological significance of the findings should be presented in the Discussion to offer reader the authors’ view on the broader implications of the work. Relevant points include:

- Do the authors believe that conformational bias in nhTMEM16 in various cryo-EM conditions may be reflective of physiological regulation? Is it likely to happen in cells in vivo?

This is an excellent point. We do hypothesize that the various observed conformation are physiological and indeed we explicitly state “…that the 7 observed conformations represent intermediates along the transition from apo closed to Ca2+ bound open” (Lines 444-445). Beyond this, we cannot speculate on whether the environmental dependent bias on nhTMEM16 can happen in a physiological context. We imagine that subtle changes in membrane composition can affect TMEM16 function, and indeed we see quite dramatic effects of lipid composition of scrambling activity, however whether these changes are reflective of shifts in the conformational landscape of groove opening, of effects of membrane properties, or both, it remains to be seen. Gaining definitive insights into this would require extensive additional structural experiments in unbounded membranes (i.e., from reconstituted liposomes of different composition or native vesicles, cell membranes) that are outside of the scope of the present work.

- Do the authors believe that such regulation may also apply to mammalian TMEM16 scramblases or even channels?

We consider this is a definite possibility, and now added a sentence stating that “This raises the possibility that unbounded membranes, such as those of liposomes, might perturb less the conformational landscape of the imaged proteins.” (Lines 499-501) However, without direct evidence we prefer to avoid speculating on this fascinating topic.

- What implications do these findings have for our understanding of lipid scrambling mechanisms by TMEM16 scramblases that work in intracellular (thinner) membranes (such as TMEM16K)?

We agree this is an important point. We now added a sentence stating “The strong dependence of closed groove scrambling on membrane properties could provide a mode of regulation of TMEM16 activity in cellular membranes, such as the cholesterol rich plasma membrane or the thinner ER membrane.” (Lines 434-436)

- What implications might the knowledge of residues involved in lipid scrambling of closed scramblases potentially have for medicine and therapy? Can the authors speculate as to whether the identified residues have the potential to be tackled pharmacologically and what use could this have?

We do not know whether the residues we identified as important for closed groove scrambling could provide a pathway to pharmacological manipulation of TMEM16 scramblase activity. This is a fascinating topic, especially in light of the very poor availability of pharmacological tools to manipulate TMEM16 scramblase activity. However, at present it remains speculative and outside the scope of the present manuscript.

More generally, what is the physiological role of lipid transport in the absence of Ca²⁺? Does this constitute a lipid "leak”?

This is an excellent question. One possibility is that scramblases have a basal activity, that in cellular homeostasis is counteracted by the activity of flippases and floppases. Alternatively (or complementarily), it is possible that in the context of an unperturbed native membrane the basal activity is negligible. However, we do not have data addressing the present point and therefore our hypotheses remain limited to pure speculations, therefore we prefer to maintain the focus of the present manuscript on the mechanism of closed groove scrambling and on the potential effects that the environment can have on the interpretation cryoEM imaging experiments.

Optional suggestions:

1. Regarding residues involved in groove opening (E313-R432), it would be very interesting to expand the work by studying additional mutants and investigating more fully the role of E313 in DOPC:DOPG lipids, since at present only a mutation in R432 was tested experimentally in this lipid composition.

We agree with the reviewers that expanding the analysis to other residues, such as E313, would be interesting. However, initial functional experiments suggested this mutant behaves similarly to R432A, and thus we did not think it would provide much additional mechanistically insights to what we already have.

2. Measurements of ion transport in nhTMEM16 would also be useful to further validate the closed groove conformation of R432A. This could shed new light onto whether ion transport and lipid transport are coupled in TMEM16 proteins.

This is an excellent suggestion, one that indeed we considered at length during this project. Ultimately, we decided not to pursue this avenue of investigations because of the limitations of the flux assay for non-specific ion channels. While flux assays can provide quantitative measures of effects for anion or cation selective channels, for non-selective channels these assays only provide very coarse yes/no answers (i.e., whether the construct mediates any channel activity or not). Since we expected these mutants might have intermediate phenotypes, rather than completely ablating channel activity, we were concerned that the experiments would be inconclusive at best or, at worst, misleading. These limitations are extensively discussed in our previous manuscripts (Lee et al., Nat Comms, 2018; Falzone and Accardi, Methods Mol Biol, 2020).

3. Since the authors found significant differences in their new structures with previously reported, how do Ca²⁺-bound closed structures of nhTMEM16 in POPC/POPG (previously published) and DOPC/DOPG (obtained in this study) compare to each other?

We thank the reviewers for this suggestion. In Lines 167-168 we now state: “The Ca2+ bound closed conformations in MSP1E3 DOPC/DOPG (PDBID: 6QMB) and MSP2N2 POPC/POPG are nearly identical (Cα r.m.s.d ~0.50 Å).”

4. The purpose of creating composite symmetric maps from symmetry expanded monomers is questionable – if it is not possible to isolate this symmetric state by classification approaches, it is probably very transient, or not present at all. However, there are no strict guidelines, and it is acceptable as long as everything is described in MM and all the maps deposited. Are composite and monomer E3D1 apo maps deposited alongside the main map as EMD-41477?

We agree with the reviewers that depositing the maps of the unexpanded dimers is appropriate and opportune, and indeed we did so

i. the combined dimer map which was primarily used for model building is deposited as EMDB: 41453 and the model as PDB: 8TOI;

ii. the local refined monomer map was deposited as EMDB: 41458

iii. the dimer consensus map used for map combination was deposited as EMDB: 41457

The rationale to generate a combined dimer map is that this allows for a better visualization of the protein-bilayer interface and the ensuing distortions. When viewing the map of a single monomer it is difficult to appreciate these effects.

5. The authors show that Ca²⁺-dependent α6 straightening is important for closed-groove scrambling. This is directly relevant for TMEM16F, for which this is the only conformational change observed. The authors note that extracellular α4 is more mobile in R432A mutant, is this in any way similar to the conformations reported for more active TMEM16F mutants (Arndt et al., 2022)?

What we see is that the density for the top of TM4 becomes very weak. This is quite different from what Arndt et al. reported, where they see a significant and defined movement of both TM4 and TM3. While we think many of the basic mechanisms of closed-groove scrambling we and many others are beginning to unravel are likely conserved across TMEM16 homologues, it is very likely that differences will exist between homologues. We now make this important point in Lines 432-434.

(This is a response to peer review conducted by Biophysics Colab on version 1 of this preprint.)

Consolidated peer review report (11 October 2023)

GENERAL ASSESSMENT

The TMEM16 protein family is composed of ten members in mammals, and fewer in lower eukaryotes. Members within this protein family play remarkably different roles: some serve as Ca²⁺-activated ion channels, others work as lipid scramblases in a Ca²⁺-dependent manner, and some combine the two functions. The molecular determinants responsible for lipid transport in TMEM16 scramblases are not fully defined. The current view of lipid scrambling is that, in presence of Ca²⁺, TMEM16 scramblases change their conformation to expose a hydrophilic ‘groove’ to the membrane. This destabilizes the lipid bilayer, enabling translocation of lipids (e.g. phosphatidylserine) from the inner to outer leaflet of the membrane. However, recent evidence suggests that scrambling can occur even when the hydrophilic groove is closed.

The new study by Feng and colleagues aims to investigate the molecular basis of closed-groove scrambling using the fungal scramblase, nhTMEM16. This protein was previously reported to maintain closed groove conformations even in the presence of Ca²⁺. The authors resolved a series of WT nhTMEM16 structures in two different nanodisc scaffolds, as well as several mutants with impaired scrambling. Strikingly, the conformational landscape of nhTMEM16 was found to rely on the lipid composition and scaffold used: the smaller E3D1 scaffold favored closed groove states and the larger 2N2 scaffold permitted intermediate and open-groove conformations. A high-resolution closed-groove structure obtained in E3D1 allowed the identification of a continuous file of lipid molecules around the catalytic groove region, providing a structural basis for lipid interaction with the closed groove. This complements prior work from this group involving a closely-related homolog, afTMEM16, in which the authors were able to visualize lipid molecules around the open groove. Furthermore, the authors succeeded in capturing three novel states of nhTMEM16 (Ca²⁺-free closed, Ca²⁺-bound intermediate-open and Ca²⁺-bound wider open states), completing the picture of conformational transitions that this protein undergoes upon activation.

Mutation of key residues interacting with outer leaflet lipids selectively impaired scrambling in the absence of Ca²⁺. Residues involved in groove opening (E313-R432) were also identified and a mutation at this site (R432A) locked the nhTMEM16 scramblase in a closed-groove conformation, providing new insights into residues critical for groove opening. Furthermore, the authors tested the activity of nhTMEM16 mutants in several lipid compositions and reported striking differences, clarifying discrepancies from the authors’ prior work on nhTMEM16 using different lipid compositions and consolidating some of the observations from other TMEM16 homologs. It is noteworthy that the authors probed the effect of nanodisc size and lipid composition on nhTMEM16 conformation, providing thought-provoking insights for the membrane protein field. This approach is particularly valuable for closed-groove mutant structures, to ensure that the observed conformation is not dictated by scaffold size.

Overall, this is a piece of carefully executed experimental work. The results are interpreted carefully in the context of the published literature, and the work provides important insight into plasma membrane lipid homeostasis. While the study does not have technical weaknesses, it could be improved in its presentation in order to make it more accessible to readers who are not experts in the TMEM16 field.

RECOMMENDATIONS

Essential revisions:

1. For readers not familiar with the field, some technical details might need to be explained in greater detail. For example:

- In the section “Residues coordinating outer leaflet lipids are important in closed groove scrambling”, please indicate the method of measuring scrambling (liposome-based activity assay etc.) and refer to some of your prior work where the method is described for readers not familiar with the TMEM16 field. Additionally, it needs to be stated clearly what is considered a significant change in scrambling, as liposome assays are usually quite variable.

- Since prior work done by the group indicates that membrane thinning is a determinant of scrambling, and an open groove further thins the membrane to potentiate scrambling, it is not intuitive why the R432A mutant scrambles with WT-like rates in the presence of Ca²⁺. If this is due to the limitation of the assay (e.g. rate of NBD lipids bleaching), this should be stated more explicitly. Do the authors have insights from their structures regarding membrane thinning by R432A with/without Ca²⁺ and how that compares to WT protein?

- It is difficult to follow the reasoning for the R432A+Y327A/F330A/Y439A mutant phenotype. Is the assumption that Y327A/F330A/Y439A is in the open conformation with Ca²⁺, and therefore adding a mutation stabilizing the closed groove impairs scrambling in presence of Ca²⁺?

- What the authors believe about the lipid pathway when the groove is open should be discussed in more detail and with reference to Alvadia et al 2019.

2. A more detailed account of the physiological significance of the findings should be presented in the Discussion to offer reader the authors’ view on the broader implications of the work. Relevant points include:

- Do the authors believe that conformational bias in nhTMEM16 in various cryo-EM conditions may be reflective of physiological regulation? Is it likely to happen in cells in vivo?

- Do the authors believe that such regulation may also apply to mammalian TMEM16 scramblases or even channels?

- What implications do these findings have for our understanding of lipid scrambling mechanisms by TMEM16 scramblases that work in intracellular (thinner) membranes (such as TMEM16K)?

- What implications might the knowledge of residues involved in lipid scrambling of closed scramblases potentially have for medicine and therapy? Can the authors speculate as to whether the identified residues have the potential to be tackled pharmacologically and what use could this have? More generally, what is the physiological role of lipid transport in the absence of Ca²⁺? Does this constitute a lipid "leak”?

Optional suggestions:

1. Regarding residues involved in groove opening (E313-R432), it would be very interesting to expand the work by studying additional mutants and investigating more fully the role of E313 in DOPC:DOPG lipids, since at present only a mutation in R432 was tested experimentally in this lipid composition.

2. Measurements of ion transport in nhTMEM16 would also be useful to further validate the closed groove conformation of R432A. This could shed new light onto whether ion transport and lipid transport are coupled in TMEM16 proteins.

3. Since the authors found significant differences in their new structures with previously reported, how do Ca²⁺-bound closed structures of nhTMEM16 in POPC/POPG (previously published) and DOPC/DOPG (obtained in this study) compare to each other?

4. The purpose of creating composite symmetric maps from symmetry expanded monomers is questionable – if it is not possible to isolate this symmetric state by classification approaches, it is probably very transient, or not present at all. However, there are no strict guidelines, and it is acceptable as long as everything is described in MM and all the maps deposited. Are composite and monomer E3D1 apo maps deposited alongside the main map as EMD-41477?

5. The authors show that Ca²⁺-dependent α6 straightening is important for closed-groove scrambling. This is directly relevant for TMEM16F, for which this is the only conformational change observed. The authors note that extracellular α4 is more mobile in R432A mutant, is this in any way similar to the conformations reported for more active TMEM16F mutants (Arndt et al., 2022)?

REVIEWING TEAM

Reviewed by:

Anna Boccaccio, Senior Research Scientist, Istituto di Biofisica, Italy: electrophysiology, biophysics of channels and scramblases

Valeriia Kalienkova, Postdoctoral Researcher, University of Bergen, Norway: membrane proteins, single particle cryo-EM

Paolo Tammaro, Professor, University of Oxford, UK: molecular and systems physiology and pharmacology of ion and lipid transport

Curated by:

Michael Pusch, Research Director, Istituto di Biofisica, Italy

(This consolidated report is a result of peer review conducted by Biophysics Colab on version 1 of this preprint. Comments concerning minor and presentational issues have been omitted for brevity.)

Authors’ response (11 February 2024)

GENERAL ASSESSMENT

Ionotropic glutamate receptors mediate the large majority of excitatory synaptic transmission in the brain. These receptors consist of four classes: AMPA, kainate, NMDA and delta receptors. NMDA receptors are obligate tetramers composed of two GluN1 and two GluN2 (or GluN3) subunits. Compared to other iGluRs, they have the particularity of requiring two different agonists for their channel to open: glycine binding on GluN1 and glutamate on GluN2.

Seljeset et al. investigate the molecular determinants controlling ligand potency and NMDAR activity at the level of the ligand-binding domains (LBDs), where the agonists bind. They identify a specific position, D732, whose mutation to either leucine or phenylalanine leads to a constitutively active GluN1 subunit, and thus to NMDARs activated solely by glutamate. This aspartate is well known in the field, since it is a highly conserved, signature residue in iGluRs that binds amino acid ligands, together with an arginine in the LBD upper lobe. Surprisingly, although glycine cannot further activate GluN1-D732L/GluN2Awt receptors, glycine site antagonists like 5,7-DCKA or CGP-78608 can still bind and inhibit NMDAR activity. This study is therefore very intriguing, as it raises new questions about something that was previously thought to be understood. By using a combination of unnatural amino acids and conventional mutagenesis, the authors propose that D732 contributes to glycine-mediated effects by changing local interactions with nearby residues. In addition, they show that this behavior is specific for the GluN1 subunit, since mutation of the equivalent aspartate in the GluN2 subunit does not yield constitutively activated GluN2 subunits. Finally, the authors identify a homomeric iGluR from the placozoan Trichoplax adhaerens, Trichoplax AKDF¹⁹³⁸³, in which this conserved aspartate is replaced by a tyrosine. When expressed in Xenopus oocytes, the channel shows constitutive activity. Mutation of the tyrosine into an aspartate, to convert Trichoplax AKDF¹⁹³⁸³ into a “classical” iGluR, decreases Trichoplax AKDF¹⁹³⁸³ constitutive current and allows this channel to be activated by glycine and D-serine. Interestingly, an adjacent residue that is a serine in most mammalian subunits is also a tyrosine in Trichoplax AKDF¹⁹³⁸³, and mutation of both tyrosines yields a glutamate-gated ion channel comparable to mammalian receptors. All of this suggests that the nature of the residue at position 732 influences not only ligand binding but also channel gating.

The study is technically sound, with appropriate controls, and uncovers intriguing properties of a position in GluN1 LBD at which specific side chain mutations can lock the subunit in an active state. Investigation of Trichoplast iGluR further reinforces these findings. This study should lead to a better understanding of how LBDs prime channel opening in iGluRs in the absence of agonists. In addition, co-agonist insensitive GluN1-D732L containing NMDARs could be used as tools to investigate the physiological consequences of NMDAR regulation by their co-agonist site. In contrast to previously engineered NMDARs activated solely by glutamate, which rely on the LBD being locked in its active state by cysteine bridges (Blanke and VanDongen, J Biol Chem 2008), GluN1-D37L/GluN2A NMDARs remain druggable (i.e. they can still be inhibited by glycine-site competitive antagonists). This is a great advantage when investigating the function of these receptors in a native context. The study identifies a few gaps that remain in our mechanistic understanding of D732’s role in channel gating. Particularly, it is unclear how subtle modification of residue side chains at position D732 lead to such drastic changes in function and why these effects are specific to GluN1 LBD. Also, why does mutation of D732 into isoleucine lead to a constitutively active GluN1 subunit, while mutation of a closely related leucine residue prevents activation of the receptor by glycine? The idea of a “hydrophobic plug” formed by D732L or D732F sidechains leading to constitutive activation would benefit from further validation since other hydrophobic substitutions (A, V, I, Y, and W) do not produce similar effects. Finally, it would be interesting to carry out further investigations of the role of the interaction between D732 and Q536 in open conformation stability. Thus, this paper puts forth interesting questions that could be addressed by future studies, for example molecular dynamics simulations and exploration of the LBD free energy landscapes (as in Yao et al., Structure 2013), to understand the impact of the GluN1-D732L mutation on GluN1 LBD conformational mobility.

RECOMMENDATIONS

Essential revisions:

1. Page 2, “These data show that essentially all substitutions at the GluN1-732 position decrease glycine potency, but leucine and phenylalanine substitutions also remove the requirement for glycine co-agonism in GluN1/GluN2A NMDA receptors”: One other hypothesis for the lack of glycine dependence of GluN1-D732I and D732Y + GluN2A receptors could be that the mutated receptors have a glycine potency so high that GluN1 LBD is already saturated by contaminating, ambient glycine. At this point in the paper, the authors cannot distinguish between one hypothesis or the other, therefore we suggest that this sentence be rephrased. Later in the text, control experiments with GluN1-R523K mutations that kill glycine binding and competition with 5,7-DCKA show that glycine-independent activation of GluN1-D732L/GluN2A mutants is not due to constitutive occupancy of GluN1 LBD by contaminating glycine.

ER1) We have now changed this to (page 4): “These data show that most substitutions at the GluN1-732 position decrease glycine potency, but leucine and phenylalanine substitutions alter GluN1 activity in such a way that leads to single-mutant NMDA receptors activated solely by glutamate.”

1. Does glycine insensitivity in GluN1-D732L/GluN2A NMDARs reflect a constitutively active GluN1 subunit or is this subunit locked in another conformational state that cannot be further modified by glycine? This could be answered by estimating the maximum open probability of GluN1-D732L/GluN2A NMDARs compared to their wt counterparts. To estimate Po, the authors could measure the kinetics of NMDA receptor current inhibition by MK801 (the slower MK801 inhibition, the lower the Po; see Chen et al., J. Neurosci 1999; Blanke and VanDongen, JBC 2008) in the presence of saturating agonist concentrations (100 μM Glu, 100 μM Gly for wt and only 100 μM Glu for mutant).

ER2) We have now assessed the rate of MK-801 block in glutamate-gated mutant and glycine + glutamate-gated WT receptors, and reshuffled text/figures, as this ties in well with ER4) below. MK-801 results now in Figure 3 on page 6, and main text on page 5: “In order to understand whether the glycine-insensitive GluN1-D732L subunit is in a constantly activated state or occupies a different conformation that may reflect an alternative to typical channel gating, we compared the kinetics of WT receptor and GluN1-D732L-containing receptor inhibition by the open-channel blocker MK-801, which can be used to evaluate maximum open probability of NMDARs ^26,30. We observed very similar kinetics of inhibition of WT and mutant receptors (Fig. 3A), indicating similar open probability in solely glutamate-gated GluN1-D732L-containing receptors and glutamate and glycine-gated WT receptors. This reflects unchanged maximum open probability in solely glutamate-gated NMDARs with disulfide-locked GluN1 LBDs assayed by single channel recordings ²⁷. This suggests that the GluN1-D732L subunit is in a constantly activated state.”

When viewed alongside high sensitivity of mutant subunits to DCKA - OS1) below - it’s difficult to conclude what sort of active state the mutant subunit adopts. We’ve assessed the best we can at the moment, and in this paper we’ll have to leave it at “here is the observation; here is some evidence ruling out various possibilities; and here is a receptor from another family that shows something remarkably consistent”. Future studies will have to establish exactly what state the mutant subunit adopts.

1. Page 4: The term “hydrophobic plug” is not fully justified since other hydrophobic residues do not lock GluN1 LBD in its active state.

ER3) We have replaced nearly all use of this term, in the title and in the main text, to e.g. “certain hydrophobic substitutions” or “L/F substitutions”.

1. Figure 2, redox sensitivity of GluN1-D732L/GluN2Awt: It would be helpful to explain the point of this experiment – maybe to investigate if the D732L mutation has an impact on the receptor gate rather than on the LBD? In any case, the authors should investigate the effect of DTT on the activity of wt GluN1/GluN2A receptors to determine whether there is an absence of an effect of the D732L mutant on redox sensitivity.

ER4) Indeed we were curious if D732L affected the gate via this allosteric route, rather than by just altering LBD conformation. And we have now shown the effect of DTT on WT receptors.

In addition to re-writing to better explain the point, as suggested, we have also re-written to follow on from new data/text on the whether the D732L mutation affects LBD, gating, etc: “We next questioned if D732L/F substitutions affect channel gating, rather than simply altering the LBD conformation. The gating machinery is complex, but it includes the peptide segment linking the C-terminal end of the LBD to membrane-spanning helix 4 (LBD-M4 linker, (11)). The LBD and LBD-M4 linker are confined by a C744—C798 disulfide, just four helical turns after D732, whose disruption by reduction enhances channel gating (28)). We considered that if the D732L/F substitution is coupled to channel gating via this route, then removal of the C744—C798 disulfide via the C744A mutation might alter glutamate-gated currents in GluN1-D732L-containing receptors. Alternatively, the typical enhancement by the reducing agent dithiothreitol (DTT) might differ in GluN1-D732L compared to WT receptors.”

And new Figure 3 now includes DTT effects on WT receptors.

1. Page 6: The authors find that mutation of Q536 decreases glycine potency and conclude there is an interaction between D732 and Q536. However, the effects of D732 and Q536 mutations could be independent, therefore the authors should consider mutating both residues together to look at the additive/non-additive effects of the mutations. Or perhaps, note in the Discussion that some sort of mutant cycle analysis or molecular dynamics simulation would be needed to rigorously test these ideas.

ER5) We have now made and tested a double mutant combining D732E and Q536N and performed mutant cycle analysis.

(We also tried to do this for Q536 side chain (regular mutations) and A734 main chain (non-canonical substitutions), but double mutants involving non-canonical amino acids at A734 were not successful – Figure S1.)

As is now shown in Figure 4D, the effects of the mutations are decidedly non-additive, yielding an Ω value of 0.05, corresponding to a reasonably high energetic coupling of ~7 kJ/mol. We have now added to the relevant section of the Results on page 8: “If an interaction between Q536 and D732 were energetically important for receptor activation, the effects of their mutations should be non-additive ³¹. We therefore tested glycine potency at double-mutant GluN1-Q536N/D732E-containing receptors and observed non-additive changes in EC₅₀, with a strong coupling value, Ω, of 0.05 (Fig. 4D). This deviation of Ω from unity, corresponding to an interaction energy of 7.4 kJ/mol is relatively high ³¹, confirming that Q536 and D732 are energetically coupled. We tried to analyse energetic coupling between Q536 and A734 via double mutants incorporating nonsense suppression at the A734 position, but unfortunately, attempts to incorporate Aah into such double mutants via nonsense suppression were unsuccessful (Fig. S1B).”

1. Page 6, “A hydrophobic plug does not cause constitutive activity in all NMDA receptor subtypes”: This title is misleading as it raises the expectation that the effect of GluN1-D732L has been investigated in the context of GluN1/GluN2A, GluN1/GluN2B, etc NMDARs. Instead, the equivalent mutation is made in the GluN2 subunit. We suggest using the word “subunit” rather than “subtype”.

ER6) We have changed this Results section title (page 8) to: “L/F substitutions do not cause constitutive activity in all NMDA receptor subunits”

1. Page 7, effect of GluN1-D732L in the context of GluN1/GluN3 NMDARs: We would not expect current to be observed with GluN1-D732L/GluN3 NMDARs, since locking GluN1 LBD in its active state desensitizes the receptors. The effect of the D732L mutation seems therefore conserved between GluN1/GluN2 and GluN1/GluN3 NMDARs. In addition, when using CGP, please cite Grand et al., Nat. Commun. 2018 since they were the first to use CGP as a tool to record GluN1/GluN3 currents.

ER7) We have now cited that paper specifically here (page 8) and inserted the following (page 8/9): “While this seems like inactivity of the mutant GluN1 subunit in GluN1(4a)/GluN3A, it could yet reflect the activity of constitutively active mutant GluN1 subunits in GluN1/GluN2A receptors, as GluN1 activity in GluN1/GluN3A receptors is known to cause more desensitization than activation (Grand et al 2018).”

1. Figure 5C: It is stated in the text that the aspartate position is “highly” conserved. However, no actual number or percentages are given for this statement. How does it compare to the residues in the highly conserved SYTANLAAF motif or other conserved positions? This sort of analysis does not need to be done for the entire receptor, but perhaps for glycine and glutamate binding residues and SYTANLAAF motif, to give a quantitative feel for statements about conservation. In addition, what other types of residues occupy this position in other species? And what was the number of species/subunits included in the analysis?

ER8) To clarify the level of conservation, we have added Table 1 (page 10) listing the % conservation of amino acids at selected positions.

In analyzing % conservation, we noticed that several iGluR sequences with gaps in the ligand-binding domain or channel-forming helices had escaped our filtering out incomplete sequences in our phylogenetic analysis. We therefore revisited our phylogenetic analysis, removed several incomplete sequences, and replaced Crassostrea gigas (a mollusc spiralian) iGluR sequences with Schmidtea mediterranea (a flatworm spiralian) sequences. This (1) means less sequences with gaps in the ligand-binding domain in our alignment/tree and (2) better covers the diversity of the lineage Spiralia now that we have sequences of Lingula anatina and Schmidtea mediterranea, which are more distantly related than Lingula anatina and Crassosttrea gigas (Laumer et al 2019, PMID:31690235; Marlétaz et al., 2019, PMID:30639106).

The result is a phylogenetic and amino acid sequence analysis of 204 iGluR genes (previous version had 212 genes) with the same overall topology as the previous version, including lambda, NDMA, epsilon, and AKDF iGluR families (Fig. 5B, page 9).

The number of subunits/genes used is stated in the Figure legend. The number of and reasoning behind the number of species used is described under Methods, Bioinformatic analyses: in exploring the conservation of the D732 residue, we have not tried to use as many iGluR sequences as possible; rather we have tried to assess this residue in a broad sample covering all (animal) iGluR families and from a careful selection of different animal lineages, while also avoiding fast-evolving species like Drosophila, which complicate tree topology. Hence our description of “two ctenophores, one poriferan, etc” under Methods, Bioinformatic analyses. In the main text (Results, page 9), we retain our original description: “We assembled diverse iGluR sequences, covering all animal lineages and animal iGluR families (Fig. 6A,B)…”

1. Figure 5, panel F: From what we understand, the authors created dose-response curves for wt Trichoplast AKDF¹⁹³⁸⁶³ based on steady-state currents and for Y742D/Y743S mutants based on peak currents. If this is the case, one cannot compare the two dose-response curves since peak current potentiation and steady-state inhibition likely reflect different conformational transitions.

ER9) We acknowledge this issue and that we can’t really say that ligand-activated D742 channels bind D-serine better than ligand-deactivated Y742 channels. But we think it’s fair to point out that mutant D742 channels react (by conducting current) to micromolar ligand concentrations whereas wildtype Y742 channels react (with decreased current) only to millimolar concentrations, and we have re-written to acknowledge the issue raised for this comparison (page 11): “Finally, we tried to assess whether position 742 determines ligand potency in addition to channel activity in AKDF¹⁹³⁸³ receptors. For these experiments we employed D-serine, as recovery from glycine-induced deactivation (Fig. 6C, far-left) and activation/desensitization (Fig. 6C, far-right) was very slow. Substantial deactivation of WT receptors was only induced by millimolar D-serine concentrations, whereas Y742D-containing mutants were activated by micromolar concentrations (Fig. 6D,E), with an EC₅₀ of 490 ± 120 µM at Y742D/Y743S (n = 4; Y742D EC₅₀ not assessed due to slow recovery from desensitization). Our measure of potency is confounded by the fact that deactivation (in WT channels) and activation (in mutant channels) are presumably coupled to D-serine binding via different conformational transitions. Nonetheless, we observe that a naturally occurring large hydrophobic side chain at the top of the β-strand preceding the αI helix leads to an AKDF homo-tetramer that shows constitutive activity and responds only to millimolar concentrations of D-serine. In contrast, “re-introducing” an aspartate to this position reinstates more typical ligand-dependent activation and sensitivity to micromolar concentrations of D-serine.”

Optional suggestions:

1. Figure 2, glycine/DCKA competition: It is difficult to understand how a GluN1 LBD-locked closed (active state) could still bind DCKA. If the open-to-close equilibrium of GluN1 LBD is displaced towards its closed state, then DCKA Ki should be shifted to the right compared to wt receptors. Additionally, DCKA inhibition kinetics should be slower if DCKA needs to “wait” for rare resting-like conformational changes to bind. Did the authors investigate DCKA potency and inhibition kinetics?

OS1) We have now investigated DCKA potency. DCKA capably inhibits GluN1-D732L/GluN2A-WT activity, and perhaps surprisingly, potency of DCKA at the mutant is greater than at wildtype. We suspect this is due to (1) the introduction of a hydrophobic leucine residue right next to an aryl group of DCKA, increasing DCKA affinity directly, (2) the absence of glycine binding to this site, so no need for competition, and (3) potentially other mechanisms such as cooperativity between subunits. Again, establishing the precise nature of our mutant LBD conformation here is for future structural and molecular dynamics studies. But we have described the results, along with our following interpretation, (page 4): “Whether increased DCKA potency in GluN1-D732L subunits derives from the now non-competitive nature of the inhibition in mutant receptors or from the introduction of a favourable hydrophobic interaction with the dichlorobenzene moiety of the inhibitor is unclear. But the high DCKA potency would suggest that the constitutively active GluN1-D732L subunit is, unexpectedly, not due to a permanently clamshell-closed LBD in the mutant. This may reflect the fact that extent of LBD closure is poorly correlated with agonist efficacy in GluN1 subunits, in contrast to AMPA receptor GluA2 subunits ²¹.”

1. The authors show in many panels that GluN1/GluN2A currents desensitize (e.g. Fig.1B, 3C, 4A). In Xenopus oocytes, NMDAR currents do not normally desensitize. We fear this desensitization might stem from contamination of the NMDA current by calcium-activated chloride channels, which can be activated by high quantities of barium when large NMDAR currents are measured. To avoid this problem, we advise that NMDA currents above 2 µA are avoided.

OS2) We have moved forward presuming that potential changes in current amplitude due to a small chloride flux doesn’t affect our measures of potency or ligand-selectivity. But in our new experiments, we’ve especially tried to avoid large currents.

1. Page 5, investigation of D732 state-dependent interactions: Mutation of residues near D732 to unnatural amino acids to replace the peptidic NH do not bring much information about the mechanisms of D732 action. The fact that the 734Aah and 735Vah cannot mimic the effect of the D732L mutation could be due to many factors, including the fact that changing the peptide bond probably changes the local structure of the LBD. Perhaps mention this in the discussion.

OS3) We have now acknowledged this possibility in the Results, right after we describe the decrease in glycine potency caused by the 734Aah mutation (page 7): “Although this may be due to local conformational changes due to altered main chain structure,…”

1. It is intriguing that the D732L mutation locks an active conformation of the GluN1 subunit but not the GluN2 subunit, suggesting two different mechanisms of LBD closure by glutamate and glycine. It would be interesting to look at the effect of the equivalent mutation on the GluN3 subunit to investigate if this locking effect is specific to glycine-binding LBDs or just to the GluN1 subunit.

OS4) We have now made and tested mutant GluN3A subunits D485L and D485F. Simply decreases glycine activity altogether (reflecting the effects of the mutations in GluN2A). Described on page 9: “Similarly, at oocytes injected with GluN1(4a)-WT and GluN3A-D845L or -D845F mRNAs, we saw no response to glycine alone or glycine in the presence of CGP 78608 (Fig 5D). Together, these results indicate that the induction of a constitutively active state by the D732L/F substitution is an exclusive feature of the GluN1 subunit, and the only conserved feature of the mutation in different subunits is a decrease in agonist potency.”

1. Page 9: Discussing the position of residue side chains from structures with 4 Å resolution does not seem relevant and would benefit from a caveat.

OS5) We want to retain our comparison of experiments with available structural data, so we have kept this but re-written to more openly acknowledge the caveat (page 12): “Indeed, in a cryo-electron microscopy (cryo-EM) study of GluN1/GluN2B receptors, D732 has only swung toward the ligand and away from A734 in a second of two putative pre-gating step structural models, although this is speculative considering the poor resolution of D732 side chains in those cryo-EM maps (12).”

1. Page 10: We don’t understand the point that the authors want to make with the activation of Aplysia californica. Please clarify.

OS6) He we were trying to say that “not much is required to change NMDARs from requisite co-agonism to single-ligand agonism”, either (a) in the lab via the D732L mutation or (b) naturally, as invertebrate NMDA receptors apparently show single-ligand agonism (results on invertebrate NDMARs in the literature). Further, we want to say that “by extension, we wonder if (c) in certain physiological situations, vertebrate NMDARs might indeed need only a single ligand.” We acknowledge this was unclear and – although it’s still speculative – we have now changed to (page 13): “Our work shows that only small changes in the GluN1 LBD are required for solely glutamate-gated currents in vertebrate GluN1/GluN2 receptors, and previous work suggests that invertebrate Drosophila melanogaster and Aplysia californica GluN1/GluN2 receptors can be activated by single ligands ^50,51. This suggests that NMDA receptors’ requirement of co-agonism is easily alleviated by certain mutations or conditions. As iGluR-modulatory proteins vary across cell types or even across neuronal compartments ^52,53 and NMDA receptor sequence varies across animals, it is foreseeable that in certain physiological settings, certain NMDA receptors might be activated by glutamate alone. But in most settings, certainly in vertebrates, it seems that glutamate-induced activation of NMDA receptors relies on a system of ambient glycine or D-serine ^54,55.”

1. In iGluRs, constitutive currents are often induced by mutations in the gate region, near the SYTANLAAF motif (e.g. lurcher mutations). Does the sequence around the gate of Trichoplast AKDF¹⁹³⁸⁶³ predict channel constitutive activity?

OS7) Our results with WT, single mutant Y742D, and double mutant Y742D/Y743S Trichoplax AKDF¹⁹³⁸³ receptors already show convincing evidence that the constitutive activity is via the Y742 and Y743 position: the tyrosine residues are unique to this leaky channel, and their mutation to more typical residues removes the leak current (Fig. 7B, page 11, revised manuscript).

But a look at upper M3 is warranted. As shown in Fig. 6C, AKDF¹⁹³⁸³ (YTANMAAFL) is quite similar to typical iGluRs (e.g. GluA2 YTANLAAFL). But one might ask about the single M/L difference in that motif, and we have therefore made and tested the M657L AKDF¹⁹³⁸³ mutant, comparing it with WT. Results show that this small M3 difference has little effect on channel activity. We have added this data in new Figure 7D and described it (page 11): “As channel activity of iGluRs also relies on the upper segment of the third membrane-spanning helix (M3, (34)), we also examined this segment in AKDF¹⁹³⁸³. AKDF¹⁹³⁸³ differs only subtly from most iGluRs with a methionine residue (M657) instead of leucine here (Fig. 6C), but we tested potential effects of this difference by mutating M657 to leucine. M657L activity was much like WT (Fig. 7D), however, confirming that divergence at Y742/Y743 and not the upper M3 segment determines the unique activity of AKDF¹⁹³⁸³.”

1. D-serine is another co-agonist that binds the GluN1 subunit. Compared to glycine, D-serine can make additional interactions with the lower lobe of GluN1 LBD. It would be interesting to look at D-serine dose-response curves in GluN1-D732L/GluN2A receptors: are these receptors also D-serine insensitive or can they be further activated by D-serine?

OS8) We have now measured the effects of D-serine on GluN1-D732L/GluN2A-WT receptors. As we now show in Figure 1B (green symbols), D-serine at increasing concentrations (100 nM through 100 μM) activates no additional current on top of the glutamate-gated current in mutant receptors. We have added to the end of the first Results paragraph (page 3): “Similarly, large currents were activated in mutant GluN1-D732L/GluN2A-WT receptors when 100 nM through 100 μM D-Serine was applied the presence of 100 µM glutamate (green in Fig. 1B).”

(This is a response to peer review conducted by Biophysics Colab on version 1 of this preprint.)

Consolidated peer review report (22 January 2024)

GENERAL ASSESSMENT

Nanobodies (Nbs) are small antibody fragments that function similarly to antibodies. The smaller size of nanobodies makes them useful tools for studying biology and potentially useful as therapeutics. Nanobodies have had a significant impact on research related to the structure and function of G protein-coupled receptors (GPCRs), a family of proteins that are the target of approximately 30% of approved drugs. Nanobodies fused to peptide agonists can potentially increase the potency and selectivity of ligands.

The manuscript by Nayara Braga Emidio and Ross Cheloha describes the fusion of peptide agonists to Nbs to create chimeric ligands that differentially modulate the molecular pharmacology of the Neurokinin 1 receptor (NK1R), a potential therapeutic target for the treatment of pain. The authors observe that Nb-peptide fusions display divergent pharmacology to that of the unfused peptides via extensive characterisation at multiple signalling pathways (cAMP, Ca2+ mobilization, direct Gq TruPATH measurements, and β-arrestin recruitment), receptor binding assays, and measures of downstream transcriptional activation. The pharmacology results show that these conjugates exhibit diverse and unexpected signalling properties, including enhanced receptor binding, high potency partial agonism, prolonged cAMP production, and altered transcriptional outputs.

However, the degree to which signalling was altered was highly dependent on the location of the epitope tag and the utilized Nbs with small alterations in the relative distance and orientation between the Nb epitopes and peptide binding sites, causing significantly different outcomes. These findings highlight the potential of nanobody conjugation for creating compounds with biased agonism, extended duration of action, and improved transcriptional responses, suggesting their promise for research on GPCR signal transduction mechanisms. This study also lays the groundwork for important considerations regarding optimising nanobody-peptide fusions. Importantly, for peptide discovery, these approaches may afford improved properties regarding selectivity and duration of action. Overall, this work suggests an opportunity to create long-acting agonists with enhanced signalling properties using nanobody-peptide conjugates. However, this would require further experiments to validate the mechanism of the altered pharmacology responses of the Nb conjugates.

RECOMMENDATIONS

Essential revisions:

1. Because no known Nbs bind to WT NK1R, the authors have fused the epitopes of three different Nbs (6e, alpha, BC2) to the N-terminus of NK1R. These epitope tags could alter the pharmacology of the endogenous ligand Substance P (SP) with respect to the WT receptor. A comparison of signalling for WT versus the epitope-tagged NK1R in Figure 1C would alleviate these concerns.

2. The expected masses of the Nb conjugates after sortagging are sometimes over or under the expected masses (Table S2). Could the authors clarify the reason for these differences in the text.

3. Based on the results of Figure 2, all Nb conjugates, including the negative control NbGFP-peptide, negatively impact signaling by reducing efficacy in cAMP production (which is completely abolished for Nb-SP6-11) and reducing potency in β-arrestin and Gq activation. This could be due to differences in the binding of conjugated NKA compared to non-conjugated NKA due to conformational constraints or by hindering access of the peptides to the orthosteric pocket. In addition, it is unclear if the Nbs alter NK1R signaling on their own or if they act as allosteric modulators. These concerns could be experimentally addressed in both functional and binding experiments using 1) unconjugated Nbs and 2) unconjugated Nbs and peptides.

4. Compared to the Nbalpha-NKA and Nb6e-NKA conjugates, NbBC2-NKA has no effect in the cAMP assays (no increase in potency or effect in washout experiments). This is despite NbBC2-NKA having the greatest effect in binding experiments (Figure 3A,B). Can the authors discuss these differences, particularly with respect to the conclusion that a bitopic binding mechanism may contribute to prolonged signalling.

5. Regarding biased agonism as a potential advantage of Nb-peptide conjugates, the kinetics of β-arrestin recruitment or activation should also be measured (Figure 3) to determine if there is prolonged arrestin activation or receptor internalization.

6. The impact of Nb conjugation on ligand competition binding assays was assessed in Figures 3A and 3B. However, it would be useful to include the unconjugated Nbs as a control to determine if the enhanced inhibition is due to increased hindrance to the orthosteric pocket (see comment #3) or due to increased binding of the Nb-peptide conjugates as suggested. Similarly, in Fig S10, the lack of inhibition by spantide with the Nb6e-NKA could be due to reduced access of spantide to the orthosteric pocket in the presence of the Nb conjugate due to steric hindrance and testing with unconjugated Nb6e would strengthen the results.

7. The kinetics of cAMP signaling are assessed in Figures 3C and 3D. An EC10 concentration of G3-NKA was compared to an EC100 concentration of the other ligands, which may not be appropriate for comparisons of kinetics in this washout experiment. Do the authors have an explanation for comparing different concentrations?

8. In the cAMP washout experiments, cAMP production was still increased after washout (Figure 3C). Can the authors discuss why this was observed (Figure 3C).

9. In the transcriptional reporter assays (Figure 4), can the authors clarify why ~35nM was chosen as the concentration of peptides?

10. There are significant caveats with the Figure 5A model provided that the authors do not mention or address. Importantly, whilst AlphaFold 2 is useful for predicting the structure of well-ordered proteins, the relative location & orientation of these domains is unreliable when there are large flexible linkers between them; as is the case with the NK1R N-terminus. It would be at least worth mentioning this, and at best doing additional MD simulations to show the relative orientation of these two "domains". In addition, the authors should discuss the effects various linker lengths between the Nbs and peptide would have.

11. If the author's suggestions are true about the relative position of the epitope tag in relation to the peptide binding pocket, this could be demonstrated by making a construct where the epitope positions are swapped. Alternatively, instead of using 3x epitope-tagged constructs, single-tagged epitope NK1R constructs should demonstrate this.

12. There is no mention of the relative affinity of the Nb:epitope pairs and how this might influence the observed pharmacology, in particular the binding experiments with washout and readouts of transcriptional activation. This should be considered by the authors.
13. With respect to therapeutic relevance, how does the prolonged cAMP production or enhanced transcription correlate with their activity in pain? NK1R is a pro-nociception receptor, does this mean we need the reversed compounds or antagonists to inhibit the receptor activity? Clarification would be appreciated.

Optional suggestions:

1. In several instances, the authors have chosen to show a representative concentration-response curve rather than showing data that are grouped across multiple replicates (e.g. Fig S4). Consider grouping data, as is often done in the field.

2. In Figure S2, it is unclear which receptor construct was used in these experiments to validate the signalling of the G3-peptides. In some of the concentration-response curves (Gs Glo, Gq TRUPATH), the maximal response is not reached, and this could affect the estimation of EC50 values reported. In any case, the authors report that G3-SP6-11 has a 100-fold increased potency, indicating that the truncation of SP might already be unfavourable for signalling. Untruncated SP could be added for comparison and may have been a better choice of ligand to see whether Nb conjugation can, in fact, improve the natural NK1R agonist.

3. In Figure 1D, the binding of the unconjugated Nbs to the tagged receptor was tested. It would be useful to compare the binding of unconjugated Nbs with peptide-conjugated Nbs to see whether a second binding point by the peptide increases total binding.

4. Fig S5 shows a lot of variability between replicates in the association of the unconjugated Nbs, is this of concern?

5. The opposite effect of nanobody-fusion with SP6-11 in regard to the washout experiments compared to NKA are striking but somewhat confusing. Ideally, a longer linker between the fusion should be used to show that this is indeed due to steric restraint altering the peptide binding pose.

6. Despite the quicker washout of the Nb-fused SP6-11 peptide, there was no significant decrease in Gq-mediated transcriptional response (Fig S11). This is difficult to reconcile, given the conclusions drawn for Nb-fused NKA (opposing effects). Is this a dose issue? The authors should explain this further.

7. At the end of the article, there is an emphasis on the potential usefulness of translational therapeutics. It would be ideal if the authors could further expand upon the likelihood and criteria for a nanobody that would recognize the WT NK1R and could act as a peptide fusion tool i.e. how much solvent accessible surface away from the peptide binding pocket is available for NK1R, and how likely it would provide the relative distance given the findings of this work.

REVIEWING TEAM

Reviewed by:

Reviewer #1: molecular pharmacology of pain-related GPCRs

Reviewer #2: structure and pharmacology of GPCRs

Reviewer #3: structure and pharmacology of pain-related GPCRs

Curated by:

David Thal, Senior Research Fellow, Monash University, Australia

(This consolidated report is a result of peer review conducted by Biophysics Colab on version 1 of this preprint. Comments concerning minor and presentational issues have been omitted for brevity.)

Authors' Response (15 August 2023)

GENERAL ASSESSMENT

The preprint by Bassetto Jr et al. presents an elegant and pioneering technique to rapidly manipulate membrane temperature and study the temperature dependence of ion channel currents. The work is a tour de force that combines the cut-open oocyte voltage clamp technique with laser illumination to achieve heating. Upon exposure to a laser pulse, the sub-membrane melanosome layer heats up, and the ensuing changes in membrane temperature are calculated from the observed changes in membrane capacitance (Cm) using a quasi-linear relationship between membrane capacitance and membrane temperature in the 15 to 45 ºC range. The approach enables the authors to achieve ~10 ºC temperature jumps within 1.5 ms and maintain the achieved test temperature for up to 150 ms. Recordings of Kir1.1, TRPM8, and TRPV1 channels are used to validate the technique. The rationale and the in situ detection of membrane temperature changes with ms time resolution is novel, and represents an important technical advance to study kinetic behavior of thermally-sensitive ion channels. Its great advantages notwithstanding, there are some limitations of the new technique in comparison with steady-state bath heating in that 1) In its current form it can be used only on Xenopus oocytes membranes (which contain melanosomes), and 2) In the cut-open setup it can be used only for the study of macroscopic, but not single-channel, currents. Also, the implementation details would benefit from some extra explanations as discussed in the recommendations below.

RECOMMENDATIONS

Essential revisions:

1. Based on the experimental arrangement, it is unclear whether the temperature indeed increases homogeneously over the entire dome-shaped membrane area from which the current is recorded. The hemispherical membrane surface is exposed to a homogeneous laser that illuminates a major portion of the top dome in the top chamber, not the complete area of the clamped membrane. Thus, at the periphery, the absorbed power per unit membrane area is expected to be smaller than around the center of the dome. In this case, the membrane capacitance would be a mixture of capacitances for areas of membrane under varied temperatures: some time-variable and others constant. The channels in all these areas are mixed. Is there a way to estimate these fractions? How quickly does the heat transfer from the shined area to the dark area, and what is the temperature gradient at the boundary area? Given the shape of the beam and curvature of the domed membrane, it is not straightforward that the curved membranes are heated evenly. Can this be tested? There are three immediate heat sinks in the setup – the external solution, the cytosol, and dark membrane (not shined). It would be helpful to estimate or discuss how these affects the temperature clamping, local temperature gradients, and the speed of Tjump.

To address this, we performed new experiments using a thermal camera to assess the homogeneity of heating during Tjumps. We observed near identical heating of the center pixels, while pixels at the edge of the illuminated area were on average \< 1 C cooler. We now show these data in a new supplemental figure (Fig. S8) and refer to it in the results and methods section. We believe these new data support our claim that the oocyte dome experiences a homogeneous increase in temperature during Tjumps with our illumination conditions.

1. Because of varying Rm, it is not clear how Tsteps can be accurately determined and be clamped at the target temperatures in real-time, without feedback as shown in Figs. 3 and 4. The empirical adjustment of h and the frequency of laser pulses is mentioned, but it remains unclear how this can be generally applied to different oocytes on a regular basis.

We agree with the reviewers that the Tstep method does not provide precise temperature control, as could be achieved using feedback control. Our approach empirically determines a laser modulation that achieves the desired Tstep, which works for oocytes expressing the same construct from the same frog. We better explain this empirically determined laser modulation for Tsteps in the revised manuscript.

1. The laser pulse method is used to elicit brief temperature jumps and "sustained" temperature steps lasting up to 150 ms. However, the gating of many temperature-sensitive ion channels is slow, with burst and interburst durations in the seconds (or tens of seconds) range. For such ion channels, much longer time periods at a given temperature are required to allow the channel population to relax to an equilibrium. Would the method presented here be suitable for generating test temperatures that are stable for seconds or tens of seconds?

Our current Tstep method is limited to durations on the order of hundreds of milliseconds due to the empirical determination of the laser modulation pulses and the fact that for long durations, short laser pulses are required every ms. This produces fluctuations on the membrane temperature. In principle these issues could be addressed using continued illumination and controlling the light intensity directly, which would allow for longer stimulation at a constant temperature.

1. To express membrane capacitance from the imaginary part of the membrane impedance, an approximation (Eq. 3) is used. The approximation is shown to hold under conditions of a resting membrane, i.e., when no ion channels are activated and thus the membrane resistance is large (~1 MΩ). Does the approximation hold also under conditions when large ionic currents are activated and Rm falls to \<0.01 MΩ?

This is an excellent point. To address it, we tested the method using only the imaginary part of the impedance to determine capacitance over a wide range of frequencies (Fig. S4). Considering values of Cm of 18.2 nF and Rm 1.17 MΩ W. We find that for frequencies larger than 300 Hz the term (𝜔𝐶𝑚𝑅𝑚)2 >> 1, which allows us to approximate the capacitance from the imaginary part of the impedance. Using Equation 7 thus follows that if Rm decreases 10 times the frequencies should increase 10 times for the approximation to hold. If Rm falls to \<0.01 MΩ it might be better to fit the total impedance (real + imaginary) as in supplementary figure 7. We must point out that we adjusted and measured the capacitance in voltage ranges where the expressed channel is not conductive.

1. For a temperature jump from 13 to 18.7 ºC (e.g. in Fig. 2), the membranes and channels might be expected to undergo an endothermic process, and thus dH > 0, not \< 0, would be expected. In this case, dE / dS = T > 0 ==> dS > 0. Relief of inactivation was proposed and interpreted as increased dislodging of the internal blocking cations with higher entropy. On the other hand, the origin of these thermodynamic parameters may be complex. Can the authors comment on the derived thermodynamic values for Fig. 2d? Also, given that the system is unlikely to be at equilibrium, it may be simpler to just report phenomenological descriptors such as Q10.

The thermodynamic parameters we derived for the relief of rectification in Kir1.1b may originate from complex processes that are difficult to interpret mechanistically. The ΔH values reported are obtained by fitting the V1⁄2 values using equation 4. Due to the fast blocking of Kir channels by internal polyamines (faster than the speed of our voltage clamp), we can consider the system at equilibrium during the temperature jumps. We explain these results mechanistically in the following paragraph:

"The rectification of Kir channels arises from the block of the pore by cytoplasmic polyamines and magnesium. The block of the channel would produce a decrease in the entropy of the blocker molecule. This entropy change needs to be offset by an enthalpy change for the blockage to be reversible. The interaction between the positive charges of the blocker with negatively charged amino acids and substantial hydrophobic interactions within the internal vestibule may contribute to these large enthalpic changes and thus explain the temperature dependence observed.

1. For the sinusoidal wave measurements and the determination of Cm in real time in a quasi-stationary circuit with a short period (say 1 ms), it is helpful to estimate the accuracy of phase-shift measurement with a limited number of data points in such a short period, and the size of errors in Cm measurements.

Since we sample the current and voltage at 1MHz we don't expect any problems due to sampling. To test our approach using the Hilbert transform to extract the capacitance at times shorter than the period of the voltage wave, we simulated an RC system in which we simulated a rapid change in capacitance, modeled after the change in capacitance from a 1 ms temperature jump (Figure S5.). We can observe that the Hilbert transform method can follow the change in capacitance accurately in these cases.

Optional suggestions:

1. The data in Fig. 1f demonstrate a substantial difference between the temperatures measured using a calibrated pipette positioned at ~1 um from the membrane and that reported for the membrane itself by the capacitance-based temperature measurement (CTM) method. That difference suggests a steep spatial temperature gradient along the membrane normal. Might such a microscopic temperature gradient affect the function of ion channels or membrane proteins in general?

The temperature gradient shown in Fig. 1f does suggests a microscopic gradient along the membrane normal during heating. From our simulations, it is not plausible that a significant temperature drop across a nanometer-length scale would occur. It is important to note that we expect that the temperature does not change at the _ membrane _. Of course, we acknowledge that small variations are possible, but we don't expect that to be significant. The difference between the measurement by the pipette and the capacitance is that the pipette is placed near the oocyte (μm), which is different from the capacitance that measures at the membrane. This is main reason for the different values for the temperature when measured with these two different methods.

1. In Extended Data Fig. 3a, the recording was done at a holding potential of -80 mV (Vm = constant). As the capacitance change over time is nearly linear during the period of "Laser On", the current I(t) = d(Cm Vm)/dt = Vm * d(Cm)/dt is expected to follow the Cm(t) change, and be at a nearly constant level. During this period, the Iop shows a sharp ON phase and a decay. It would be helpful to readers if these two phases are explained, are compared side-by-side with the data in Fig. 1e, and used to highlight the advantages of Cm measurements using sinusoidal waves.

The sharp ON phase occurs because the melanin layer quickly absorbs the laser pulse energy, creating a rapid temperature jump at the membrane. This fast heating causes a transient capacitance change that manifests as a large ON current (I=V dC/dt). After the initial spike, the temperature and, consequently, the capacitance reaches constant value state where the incoming laser energy balances the heat dissipation into the surrounding solution. During this phase, the capacitance doesn't change. Thus there is no optocapacitive current. We included a paragraph to explain this:

"This pulse protocol produces a large optocapacitive current during the temperature rising phase. Since the subsequent laser pulses maintain the temperature constant, they do not produce large optocapacitive currents."

1. It would help if the authors clarified how the speed of T steps (which the authors report is 1.5 ms for a 9 ºC jump) is expected to change with the magnitude change in temperature.

For a given laser power density, the speed of the temperature jump will depend on how much the temperature needs to rise and how quickly the heat dissipates (which depends on factors like heated membrane area, the distance of the melanin to the membrane, etc.).

In general, we empirically adjust the laser power for different magnitude temperature jumps to achieve a rapid jump in ~1-2 ms. The exact relationship between temperature jump speed and magnitude is complex and would require extensive modeling and calibration and can be seen in detail in Shapiro et al. 2012 (https://doi.org/10.1038/ncomms1742).

However, in practice, we can achieve rapid jumps over a wide temperature range by empirically tuning the laser power as needed.

1. For Tjumps in channel-expressing oocytes in Fig. 2, the T jump is measured separately, not in real-time with the voltage-series. It would be helpful as a control to show the residual currents in the presence of Ba2+ at say -100 mV. Is there any irreversible pore blocker that can be used so that Tjumps can be done in the middle of the voltage pulses? Additionally, do membranes with high densities of channels themselves alter the capacitive measurements?

We have added a new supplemental figure (Fig. S2E) showing Kir currents before and after the Ba2+ block, with and without a Tjump. This demonstrates the isolation of the optocapacitive current for subsequent subtraction. We did not test any irreversible blocker.

We have unpublished results with Kv channels that show measuring the effect of temperature on gating currents, which can be considered as a type of capacitive current. In those cases, we are careful to do the temperature measurements at a voltage where these "extra" capacitive currents are absent.

1. The data points in Fig. 4c/d are clustered together. It will be helpful to have data points at T = 13.5 and 21.5 ºC in Fig. 4c and at T = 24 and 34 ºC in Fig. 4d to show a broad range of temperatures, and compare the data with the steady-state data from the same types of oocytes clamped at these temperatures by bath perfusion.

We did not test bath temperature changes on TRP channels.

1. In Fig. 4, a plot of log(I/Imax) vs. 1/T2 at different voltages would be helpful to illustrate its connection to the enthalpic changes (Equation 6).

Since we have deemphasized the van't Hoff analysis in the revised manuscript, we opted not to include these specific plots. However, it could provide helpful background, especially for readers interested in the thermodynamic framework.

1. Can the change in single channel conductance () for TRPM8 in the early phase of Tjump (Fig. 5c) be compared with conductance immediately before in order to estimate both Q10 at different voltages and H? This would be a test of the voltage-independence of channel conductance. The same for TRPV1.

Comparing the single channel conductance before and during the Tjump would allow an estimation of the Q10 and enthalpy change associated with conductance.

However, accurately isolating the conductance component is difficult, given the time resolution. For TRPs the conductance increase onset overlaps with the subsequent change in open probability during the Tjump.

While we could not reliably quantify Q10 for the conductance, we agree that this is an important question.

1. The assumption that channel gating is a 2-state process might complicate estimation of van't Hoff enthalpy/entropy parameters for Kir channels.

The two-state model we employed is a simplification for interpreting the thermodynamic parameters for Kir channel gating. These channels likely have multiple closed and open states. However, given the experimental results, this provides a valuable model to explain the temperature dependence of Kir.

1. A question that might be pertinent for the study of TRP channels, is how easily these methods can be used to probe the cross-modulation of temperature and TRP channel agonists. Capsaicin and hydrophobic ligands are likely to partition in the membrane – would that alter the membrane capacitance or capacitance vs temperature calibrations?

You raise a valid point we had not previously considered - hydrophobic agonists partitioning into the membrane could alter the capacitance relationship we rely on for calibration. Another calibration curve with those ligands at the membrane may be necessary to check whether this would affect the previously calibrated relationship However, if we performed the temperature measurement by capacitance at the beginning of the experiment before the application of any agonists this should fine.

1. Some supportive evidence that melanin addition to cell or vesicle membranes would allow this method to be used in other membranes would greatly enhance the applicability of this approach.

We agree that this is an important next step. Gold nanoparticles have been previously used to heat the membrane of neurons; similar approaches might render this technique in new preparations.

1. A side-by-side comparison of this approach with other approaches for studying temperature jumps in ion channels would be incredibly useful for many readers to visualize the relative abilities of various methods to deliver and measure temperature jumps.

(This is a response to peer review conducted by Biophysics Colab on version 2 of this preprint.)

Consolidated peer review report (12 September 2022)

GENERAL ASSESSMENT

The preprint by Bassetto Jr et al. presents an elegant and pioneering technique to rapidly manipulate membrane temperature and study the temperature dependence of ion channel currents. The work is a tour de force that combines the cut-open oocyte voltage clamp technique with laser illumination to achieve heating. Upon exposure to a laser pulse, the sub-membrane melanosome layer heats up, and the ensuing changes in membrane temperature are calculated from the observed changes in membrane capacitance (Cm) using a quasi-linear relationship between membrane capacitance and membrane temperature in the 15 to 45 ºC range. The approach enables the authors to achieve ~10 ºC temperature jumps within 1.5 ms and maintain the achieved test temperature for up to 150 ms. Recordings of Kir1.1, TRPM8, and TRPV1 channels are used to validate the technique. The rationale and the in situ detection of membrane temperature changes with ms time resolution is novel, and represents an important technical advance to study kinetic behavior of thermally-sensitive ion channels. Its great advantages notwithstanding, there are some limitations of the new technique in comparison with steady-state bath heating in that 1) In its current form it can be used only on Xenopus oocytes membranes (which contain melanosomes), and 2) In the cut-open setup it can be used only for the study of macroscopic, but not single-channel, currents. Also, the implementation details would benefit from some extra explanations as discussed in the recommendations below.

RECOMMENDATIONS

Essential revisions:

1. Based on the experimental arrangement, it is unclear whether the temperature indeed increases homogeneously over the entire dome-shaped membrane area from which the current is recorded. The hemispherical membrane surface is exposed to a homogeneous laser that illuminates a major portion of the top dome in the top chamber, not the complete area of the clamped membrane. Thus, at the periphery, the absorbed power per unit membrane area is expected to be smaller than around the center of the dome. In this case, the membrane capacitance would be a mixture of capacitances for areas of membrane under varied temperatures: some time-variable and others constant. The channels in all these areas are mixed. Is there a way to estimate these fractions? How quickly does the heat transfer from the shined area to the dark area, and what is the temperature gradient at the boundary area? Given the shape of the beam and curvature of the domed membrane, it is not straightforward that the curved membranes are heated evenly. Can this be tested? There are three immediate heat sinks in the setup – the external solution, the cytosol, and dark membrane (not shined). It would be helpful to estimate or discuss how these affects the temperature clamping, local temperature gradients, and the speed of Tjump.
2. Because of varying Rm, it is not clear how Tsteps can be accurately determined and be clamped at the target temperatures in real-time, without feedback as shown in Figs. 3 and 4. The empirical adjustment of h and the frequency of laser pulses is mentioned, but it remains unclear how this can be generally applied to different oocytes on a regular basis.
3. The laser pulse method is used to elicit brief temperature jumps and "sustained" temperature steps lasting up to 150 ms. However, the gating of many temperature-sensitive ion channels is slow, with burst and interburst durations in the seconds (or tens of seconds) range. For such ion channels, much longer time periods at a given temperature are required to allow the channel population to relax to an equilibrium. Would the method presented here be suitable for generating test temperatures that are stable for seconds or tens of seconds?
4. To express membrane capacitance from the imaginary part of the membrane impedance, an approximation (Eq. 3) is used. The approximation is shown to hold under conditions of a resting membrane, i.e., when no ion channels are activated and thus the membrane resistance is large (~1 MΩ). Does the approximation hold also under conditions when large ionic currents are activated and Rm falls to \<0.01 MΩ?
5. For a temperature jump from 13 to 18.7 ºC (e.g. in Fig. 2), the membranes and channels might be expected to undergo an endothermic process, and thus dH > 0, not \< 0, would be expected. In this case, dE / dS = T > 0 ==> dS > 0. Relief of inactivation was proposed and interpreted as increased dislodging of the internal blocking cations with higher entropy. On the other hand, the origin of these thermodynamic parameters may be complex. Can the authors comment on the derived thermodynamic values for Fig. 2d? Also, given that the system is unlikely to be at equilibrium, it may be simpler to just report phenomenological descriptors such as Q10.
6. For the sinusoidal wave measurements and the determination of Cm in real time in a quasi-stationary circuit with a short period (say 1 ms), it is helpful to estimate the accuracy of phase-shift measurement with a limited number of data points in such a short period, and the size of errors in Cm measurements.

Optional suggestions:

1. The data in Fig. 1f demonstrate a substantial difference between the temperatures measured using a calibrated pipette positioned at ~1 um from the membrane and that reported for the membrane itself by the capacitance-based temperature measurement (CTM) method. That difference suggests a steep spatial temperature gradient along the membrane normal. Might such a microscopic temperature gradient affect the function of ion channels or membrane proteins in general?
2. In Extended Data Fig. 3a, the recording was done at a holding potential of -80 mV (Vm = constant). As the capacitance change over time is nearly linear during the period of "Laser On", the current I(t) = d(Cm Vm)/dt = Vm * d(Cm)/dt is expected to follow the Cm(t) change, and be at a nearly constant level. During this period, the Iop shows a sharp ON phase and a decay. It would be helpful to readers if these two phases are explained, are compared side-by-side with the data in Fig. 1e, and used to highlight the advantages of Cm measurements using sinusoidal waves.
3. It would help if the authors clarified how the speed of T steps (which the authors report is 1.5 ms for a 9 ºC jump) is expected to change with the magnitude change in temperature.
4. For Tjumps in channel-expressing oocytes in Fig. 2, the T jump is measured separately, not in real-time with the voltage-series. It would be helpful as a control to show the residual currents in the presence of Ba2+ at say -100 mV. Is there any irreversible pore blocker that can be used so that Tjumps can be done in the middle of the voltage pulses? Additionally, do membranes with high densities of channels themselves alter the capacitive measurements?
5. The data points in Fig. 4c/d are clustered together. It will be helpful to have data points at T = 13.5 and 21.5 ºC in Fig. 4c and at T = 24 and 34 ºC in Fig. 4d to show a broad range of temperatures, and compare the data with the steady-state data from the same types of oocytes clamped at these temperatures by bath perfusion.
6. In Fig. 4, a plot of log(I/Imax) vs. 1/T2 at different voltages would be helpful to illustrate its connection to the enthalpic changes (Equation 6).
7. Can the change in single channel conductance () for TRPM8 in the early phase of Tjump (Fig. 5c) be compared with conductance immediately before in order to estimate both Q10 at different voltages and H? This would be a test of the voltage-independence of channel conductance. The same for TRPV1.
8. The assumption that channel gating is a 2-state process might complicate estimation of van't Hoff enthalpy/entropy parameters for Kir channels.
9. A question that might be pertinent for the study of TRP channels, is how easily these methods can be used to probe the cross-modulation of temperature and TRP channel agonists. Capsaicin and hydrophobic ligands are likely to partition in the membrane – would that alter the membrane capacitance or capacitance vs temperature calibrations?
10. Some supportive evidence that melanin addition to cell or vesicle membranes would allow this method to be used in other membranes would greatly enhance the applicability of this approach.
11. A side-by-side comparison of this approach with other approaches for studying temperature jumps in ion channels would be incredibly useful for many readers to visualize the relative abilities of various methods to deliver and measure temperature jumps.

REVIEWING TEAM

Reviewed by:

Sandipan Chowdhury, Assistant Professor, University of Iowa, USA: ion channel structure-function and temperature gating

László Csanády, Director of the Institute of Biochemistry and Molecular Biology, Semmelweis University, Hungary: structure-function of TRP channels

Marcel P. Goldschen-Ohm, Assistant Professor, The University of Texas at Austin, USA: ion channel structure-function and kinetics

Qiu-Xing Jiang, Associate Professor, University of Buffalo, USA: high resolution ion channel structure and functional thermodynamics

Curated by:

Marcel P. Goldschen-Ohm, Assistant Professor, The University of Texas at Austin, USA

(This consolidated report is a result of peer review conducted by Biophysics Colab on version 2 of this preprint. Comments concerning minor and presentational issues have been omitted for brevity.)

Evaluation statement (10 January 2024)

Driggers et al. is an elegant study that reports the structure of an open KATP channel complex formed from the Q52R diabetes mutation of the pore-forming subunit Kir 6.2, the sulfonylurea receptor (SUR1), and long-chain phosphatidylinositol 4,5-bisphosphate (PIP2) – a key lipid that stabilizes the open state of the channel and regulates inhibition by intracellular ATP. The structure reveals one PIP2 site related to that seen in other Kir channels as well as a second unanticipated one where the lipid snuggles into the interface between Kir6.2 and a region of SUR1 previously implicated in promoting the open state of KATP. This important finding helps to explain how PIP2 exerts such a profound regulatory influence on KATP.

Biophysics Colab considers this to be a convincing study and recommends it to scientists working on KATP and other membrane proteins regulated by PIP2.

(This evaluation by Biophysics Colab refers to version 2 of this preprint, which has been revised in response to peer review of version 1.)

Authors' response (22 December 2023)

GENERAL ASSESSMENT

KATP is a remarkably important potassium-selective ion channel that is inhibited by intracellular ATP, allowing it to serve key roles throughout the body, including regulation of insulin release from the pancreas. Driggers et al. describe an important study that reports the structure of an open KATP channel complex formed from the Q52R diabetes mutation of Kir 6.2, SUR1, and long-chain PIP2. Although earlier structures have been determined in closed, open and inactivated conformations, none have resolved where PIP2 binds. This has been an important limitation of the available structures given the key role of this membrane component in promoting the open state and influencing the inhibitory actions of intracellular ATP. The open channel structure reported here resembles a previous structure from the MacKinnon laboratory of a mutant channel that exhibits a very high open probability (G334D, C166S). The authors also show that channel opening is accompanied by a dilation of the Kir6.2 inner helix gate, in particular rotation of L164 and F168 away from the channel's pore, and by a conformational rearrangement at the interface between Kir6.2 and the TMD0 domain of SUR1.

The key advance that allowed the authors to resolve PIP2 bound to KATP appears to be the use of brain-derived long-chain PIP2, which was incubated with membranes prior to extraction of the channel protein with digitonin and purification, as well as the use of the Q52R mutant that promotes the open state. Remarkably, the structures of PIP2 bound to KATP reveals two PIP2 binding sites: one related to previously resolved sites in other Kir channels; and a new, unanticipated one where the lipid snuggles into the interface between Kir6.2 and the TMD0 helix of SUR1, a region of SUR1 previously implicated in promoting the open state of KATP. To examine the functional impact of the two PIP2 binding sites, the authors identify two positively-charged residues – one in each binding site – to neutralise by mutation to alanine, in an effort to disrupt the two putative PIP2 interactions. Indeed, they find that KATP channel currents on patch excision are very small and require much longer exposure to PIP2 to fully activate, compared to wild-type channels. Although one could question the physiological relevance of the new PIP2 binding site, that PIP2 remains bound throughout extraction and purification in digitonin solutions, and can be readily resolved in the structure, suggests that interactions of longer-chain PIP2 with both sites is quite favourable and likely to be occupied under biological conditions. One of the remarkable features of the new structures is that PIP2 binding to KATP causes a conformation change in the inhibitory ATP binding site, providing a mechanistic explanation for how PIP2 and ATP antagonistically engage to promote open or closed states, respectively. The structure also reveals how the Q52R mutant likely forms a cation-π interaction with W51 of SUR1, explaining how the diabetes mutation promotes the open state of KATP. Ultimately, further experiments will help unravel the physiological impact of the newly identified PIP2 site, as the electrophysiology presented in this structural study is understandably limited. However, that does not diminish the impact of the study.

Overall, this is an important study that helps to explain how PIP2 exerts such a profound regulatory influence over KATP, which will be valuable for future studies on KATP and of general interest to scientists investigating how PIP2 regulates other membrane proteins. The preprint is well-written, the work appears to have been carried out with rigor and attention to detail, and the authors present new conclusions and discuss them in the context of previous findings, some of which have been enigmatic until now.

We thank the reviewers for the positive evaluation of our work and helpful suggestions. We have revised the manuscript to address the essential revisions as well as additional suggestions from the reviewers. Moreover, since the preprint was posted in bioRxiv, we have conducted additional analysis of our cryoEM data and identified a closed channel conformation in which the new PIP2 binding site is occluded and the cytoplasmic domain of Kir6.2Q52R is rotated and translated away from the plasma membrane--a conformation that corresponds to an apo SUR1/Kir6.2Q52R and is similar to our previously published WT apo (no PIP2 added) closed structure. We have also performed additional mutational and functional studies to show the dependence of the gain-of-function phenotype of Kir6.2Q52R on intact PIP2 binding sites. The additional data included in the revised manuscript further strengthens the conclusions of our study.

Below we provide detailed response to the reviewers' essential revision requests and additional suggestions.

RECOMMENDATIONS

Essential revisions:

1. Most of the figures focus on a comparison of the new PIP2-bound open state for the Q52R mutant with a closed state of KATP. A more extensive structural comparison between the PIP2-bound open structure and other open structures solved in absence of PIP2 (e.g. ref 27 where Kir6.2 mutations C166S and G334D were used) would help clarify the functional roles of the putative PIP2 binding sites. A structural comparison of the PIP2 binding sites between the two open structures (apo and holo) would reveal whether the PIP2 binding sites are conserved in the absence of PIP2, for example. Such a comparison would help the general reader to understand which of the structural changes observed in the new structure have been seen before and those that have not. Another example would be to clarify the extent to which structural changes around the inhibitory ATP binding site seen here are related to those in previous structures thought to be open.

We thank the reviewers for the excellent suggestion to compare the PIP2-bound SUR1/Kir6.2Q52R structure with previous open KATP channel structures.. We have now included a comparison of the PIP2-bound SUR1/Kir6.2Q52R structure (holo) and the previously published pre-open structure (rodent SUR1-39aa-Kir6.2H175K fusion channel; PMID: 35589716) in the revised Figure S4. Note that while the open structure of human SUR1/Kir6.2C166S, G334D (PMID: 34815345) is also very similar to our PIP2-bound SUR1/Kir6.2Q52R structure, due to sequence variations in the different species of SUR1 used and an additional amino acid present in the construct (glycine at aa position 2), we have chosen to compare our structure with the pre-open rodent structure to avoid confusion in key SUR1 residues shown. In revised Fig.S4a,b, we also compared lipid density in the PIP2 binding pocket of all three open structures to highlight the difference between the long-chain PIP2 in this study, and the unassigned density in the pocket observed in the open structure of human SUR1/Kir6.2C166S, G334D (no exogenous PIP2 added) and the pre-open structure of rodent SUR1-39aa-Kir6.2H175K fusion (short-chain diC8-PIP2 added post purification of channel-containing detergent micelles).

1. It would be valuable for readers if the authors could explain their thinking about why the new PIP2 binding site is likely to be physiologically relevant. In its current form, some readers may be unconvinced about whether the new site is occupied under physiological conditions. For example, in the last paragraph of page 15, the authors acknowledge that in their previously published closed structures without exogenous PIP2, they saw lipid densities in the novel PIP2 site which they modelled as phosphatidylserines. Similar lipid densities were also seen near this site in the other published open state (see Fig. S6 in DOI:10.1073/pnas.2112267118). In the next paragraph on page 16, they also comment on the unusually low specificity of Kir6.2 towards phosphoinositides and other lipids, and the ability of purified KATP channels to open in the absence of PIP2. Given these findings, and the potentially high concentration of PIP2 incubated with the sample, is it conceivable that the new PIP2 site is not occupied under physiological conditions? What do the authors know about the molar fraction of PIP2 achieved in the final sample and how this might compare to the estimates of PIP2 abundance in native human cell membranes (0.2-1%)? Would PIP2 ever reach high enough concentrations in the membrane for this site to be bound? The authors might also emphasize that the channel was only exposed to brain PIP2 for a short time before being extracted and purified in the detergent solution, indicating that the interaction between PIP2 and the channel at both sites is quite strong and likely to be occupied physiologically.

We thank the reviewers for asking an important question about the physiological relevance of the two PIP2 binding sites. We addressed this question by introducing PIP2 binding site mutations in KATP channels expressed in native membranes, and tested the consequences of these mutations on channel activity (results shown in the revised Fig. 3). Mutating key residues involved in PIP2 binding, at either sites or both sites, markedly reduced channel activity in native membranes without exogenous PIP2. Adding exogenous PIP2 reversed the effects of these PIP2 binding-site mutations, providing strong evidence that these PIP2 binding sites have physiological roles in channel gating.

Regarding the question of whether PIP2 binds at the novel binding site under physiological conditions, our structural analysis suggests it is likely state-dependent. When the channel is in the open conformation, the new site accommodates PIP2 as shown in our PIP2-bound structure. Although other phosphoinositides also stimulate channel activity when applied to isolated membrane patches containing channels, given PI(4,5)P2 is the most abundant phosphoinositide in the plasma membrane, we suspect the site is likely bound to PI(4,5)P2 under physiological conditions. To address the frequency of PIP2 occupancy at the new PIP2 binding site under different physiological conditions (high ATP/ADP resembling high glucose, versus low ATP/ADP resembling low glucose) experimentally, alternative approaches will be needed, for example, by crosslinking channel subunits with bound lipids followed by identification with mass spectrometry, or solving channel structures in native membranes. These are studies we are very interested in pursuing.

In the current study, we were interested in maximizing the chance of capturing channels in the PIP2-bound conformation to understand the structural basis of channel activation by PIP2. Even under the experimental conditions of exogenous PIP2, we did observe conformations that likely correspond to apo structure at the new PIP2 binding site (from our additional analysis of the cryoEM data; see revised Figure S2 and S8), indicating the new PIP2 binding site is dynamic and can bind PIP2 when the channel is open, but not when the channel is closed.Although we did not attempt to compare PIP2 abundance (molar fraction) before and after incubation with exogenous PIP2 in the current study, we have previously quantified PIP2 in cell membranes from control INS-1 (a rat insulinoma) cells and INS-1 cells overexpressing PIP5 kinase and labelled with 32P using thin-layer chromatography (Lin et al., Diabetes, 2005; PMID: 16186385). The study showed a ~30-fold increase in PIP2, which was accompanied by a ~26-fold decrease in ATP sensitivity of KATP channels measured by inside-out patch-clamp recording, and a decrease in glucose-stimulated insulin secretion (GSIS) response. While the study does not directly answer whether physiological PIP2 concentrations would ever reach high enough as our in vitro experimental system, it does show that increasing PIP2 levels by manipulating an enzyme involved in PIP2 synthesis can induce abnormally high channel activity (i.e. ATP-insensitive) and reduce GSIS, resembling phenotype caused by the neonatal diabetes mutation Kir6.2 Q52R that stabilizes the second PIP2 binding site.

1. The electrophysiological data presented in Fig. 2, while corroborating the existence of a second PIP2 site, is not definitive. On page 9 of the text, the authors mention striking differences between wild-type and mutant channels in terms of "the initial currents upon membrane excision, the extent of current increase upon PIP2 stimulation, and the PIP2 exposure time required for currents to reach maximum." The extent of current increase is shown for multiple patches in Fig. 2E and the other differences are inferred from representative traces. The authors may wish to include some form of quantification for the amount of initial current and time course for data from multiple patches. For example, the authors mention "barely detectable currents" for the SUR1-K134A/Kir6.2-R176A mutant. Taking into account the difference in scale bars, the currents in the example provided don't look any smaller than the currents from Kir6.2-R176A/SUR1 channels. Given the proximity between the two sites, it seems possible that a mutation in one site could allosterically affect PIP2 binding at the other site. In principle, two mutations could independently affect PIP2 binding at the same functional site and have additive effects. Perhaps the strongest arguments in favour of two distinct functional sites come from the mutation map in Fig. 7, which nicely matches the two bound PIP2 molecules, and previous studies showing that KATP is less sensitive to PIP2 in the absence of SUR1, which forms part of the second binding site.

We thank the reviewers for this great suggestion to include quantification of initial currents and response time to maximum currents after PIP2 exposure, which is now included in the revised Figure 3.

1. The increase in current in PIP2 in Fig. 2E may represent the extent of the increase in probability of opening. However, calculating the fold increase in current depends on accurate measurements of the very small currents at the beginning of the experiment, which will be heavily affected by residual leak or noise. In the absence of any direct measurements of open probability (for example with single channels), the authors may wish to discuss these limitations in the text.

The initial currents were calculated as currents observed in K-INT solution upon patch excision minus currents measured in 1mM ATP (KATP currents are inhibited >99% at 1 mM ATP). As such, any leak currents were accounted for. We have now stated this in the electrophysiology section in Methods (page 15). For PIP2 stimulation experiments, PIP2 effects plateau with regard to channel P__o (i.e. total currents) and any further stimulatory effects are reflected by a gradual loss of ATP inhibition (which we check by exposure to 0.1mM or 1mM ATP as shown in revised Fig. 3). Patches that do not show the PIP2 plateauing effects on currents indicate potential leak, which we can confirm by exposing channels to the high affinity inhibitor glibenclamide. Patches showing significant leaks (gradual shift in baseline) were not included in the analysis.

Optional suggestions:

We appreciate the many excellent suggestions from the reviewers, and have made substantial changes in the revised manuscript based on these suggestions. They are detailed below:

1. The Kir6.2-Q52R mutation, which stabilizes the open channel, mediates its effects by interacting with W51 on SUR1 (Fig. 6). Q52R is also very close to the PIP2 headgroup in the novel binding site and thus could help stabilize PIP2. Hence, it would be interesting to test the PIP2 sensitivity of this mutant in excised patches, as in Fig. 2D,E. If PIP2 binding at the second site is favoured by the mutation, the PIP2-induced increase of KATP current should be lower than that observed in WT channels.

From the angle shown in the original Fig.6A, Q52R does appear very close to the headgroup of PIP2 in the novel binding site. However, Q52R is actually very far away from the second bound PIP2. We have now provided additional viewing angle in the revised Fig. 7a that offers better visualization of the distance to avoid confusion.

1. It would be helpful for the authors to provide a biochemical interpretation for the functional results in Fig. 2 D, E. It would seem that the two mutations, Kir6.2-H176A and SUR1-K134A, diminish PIP2 binding affinity but do not prevent PIP2 binding, as the low basal currents seen in the mutants can be rescued by increasing PIP2 concentration.

The text has been revised to better reflect the functional data (original Fig.2D,E, now shown in the revised Figure 3). It now reads (page 6 top): "To probe the functional role of the two PIP2 binding sites, we compared the PIP2 response of WT channels to channels containing the following mutations: Kir6.2R176A , which is predicted to weaken the first PIP2 binding site; SUR1K134A, which is expected to weaken the second PIP2 binding site; Kir6.2R176A and SUR1K134A, which weaken both PIP2 binding sites (Fig.3a)."

1. The discussion on the role of H175 on pH regulation is interesting, but speculative. As the H175K mutant still undergoes acid-induced inhibition (ref 39), it does not seem appropriate to state that the H175K mutant "abolishes channel sensitivity to pH" (p7). A positive charge at position H175 increases basal activity, suggesting that the cationic form of H175 mediates acid-induced activation. The structure shows two H175 rotamers but does not clarify which of these rotamers are populated at different pH values. In addition, there is no evidence to suggest that the cationic form of H175 preferentially interacts with PIP2 and that its neutral form interacts with E179 (p8). On the contrary, it seems more logical to predict that the cationic form of H175, which is positively charged, interacts with E179, which is negatively charged. It would be helpful to clarify several of these points.

We thank the reviewers for the constructive criticisms and agree our statement is too speculative in the absence of experimental evidence that the cationic form of H175 preferentially interacts with PIP2 while its neutral form interacts with E179. Accordingly, we have removed discussion on the role of H175 and instead, simply describe what we observe in our structure.

The revised paragraph now reads (page 5 top):

Interestingly, the Kir6.2-H175 sidechain exhibited two rotameric positions in the PIP2-bound SUR1/Kir6.2Q52R channel cryoEM density map: one oriented towards PIP2 in the conserved binding site and the other towards E179 in the same Kir6.2 subunit (Fig.2b). Kir6.2-H175 has been previously implicated in acid-induced activation of KATP channels between pH 7.4 and 6.8 with a pK of 7.16. Mutating Kir6.2-H175 to lysine, which mimics protonated state of H175, increased basal channel activity and abolished channel activation by pH, suggesting protonation of H175 favors channel opening. Moreover, mutating Kir6.2-E179 to Q greatly attenuated pH-induced channel activation, suggesting Kir6.2-E179 also has a role in acid activation of KATP channels. Our structural observation that H175 sidechain has interaction with PIP2 head group in the conserved site and with Kir6.2-E179 is consistent with the aforementioned mutation-function correlation studies. Since our protein sample was prepared at pH~7.5 (see Methods), which predicts H175 to be largely unprotonated based on the pK of acid activation of the channel of 7.16, it remains to be determined how protonation of H175 at lower pH that activates the channel alters interaction with PIP2 and E179 to stabilize channel opening.

1. There are many questions that come to mind that might be interesting topics to add to the discussion. What is the relative affinity of this novel site for PIP2 over other PI's and even other lipids? Given that previous attempts to establish this (e.g. cited in reference 38) may have been measuring the summed contribution of both sites, if both are functionally relevant (as the present results suggest), do the sites differ in their selectivity? Could this be a lipid binding pocket, which has been displaced by high levels of PIP2 and a locked-open channel? These are not trivial questions to answer, but they are important for understanding the relative importance of the two PIP2 binding sites for the function of KATP and it would be useful to discuss the limits of what can be reasonably concluded at this time. Some of these points might be addressed in the results while other could add to the discussion. In thinking about the roles of the two PIP2 binding sites, have the authors considered the possibility that the PIP2 site found in other Kir channels might act as a reservoir for PIP2 and that PIP2 moves to the new site at the interface with SUR1 once the channel opens?

We agree that the many topics raised by the reviewers are all very interesting and worth pursuing in the future. We have tried to include these and point out limitations of our data in relation to these questions in the results and discussion. It is our hope that the reviewers' comments will spark interest for further research related to these topics. For example, we plan to use MD simulation studies to address whether PIP2 bound at the conserved site may migrate to the novel site.

1. Page 9, lines 6-10: The authors suggest that the slower washout of long-chain PIP2 activation from excised patches compared to that of short-chain synthetic PIP2 is due to hydrophobic interactions between the longer acyl chains and KATP. However, this observation has been previously explained by the differences in the solubility of short- and long-chain PIP2 and therefore their rate of partition into and out of the plasma membrane. Is any data available to distinguish these possibilities?

We do not currently have data to distinguish these possibilities, but based on the structure it would be possible in the future to design mutations that perturb channel interaction with the acyl chains to dissect these possibilities.

1. Can the authors provide higher quality micrographs in Fig. S1 along with a scale bar. Why are three different micrographs shown? Also, this figure would probably benefit from moving some of the text embedded in the figure to a traditional legend along with a somewhat expanded description of what is shown graphically in the figure.

The different micrographs with KATP particles are included to show the different areas of the grid coated with graphene oxide. In one area, the folds of the graphene oxide layer are clearly visible.

1. In the main text when describing the results in Fig. 2D, it would be helpful for the general reader to first explain the protocol employing both low and high ATP concentrations and what value this has for assessing the impact of mutations. As it currently stands, the reader is left guessing why this expertly devised protocol was used.

We have revised the text to better explain the rationale of the recording protocol in both the Results section and Methods. Specifically, the alternating brief exposures to low and high ATP were designed to monitor the gradual decrease of ATP sensitivity during PIP2 exposure.

1. In Fig. 3 it would be helpful to align the three panels so the reader can appreciate how the structure gives rise to the pore radius plot in panel C. Also, the point made about the G-loop not changing appreciably between closed and opens states would be good to show in the structures.

We have revised this figure (now Fig. 4) according to the suggestion.

1. The G-loop was previously proposed to aid in preventing the leakage of K ions into the internal solution as polyamines block Kir channels (Xu et al, 2009 NSMB). It might be worth commenting on this as it seems compatible with what is found here in that region.

Since we do not have any direct experiments to test this, we have decided to leave out the reference in the current study.

1. Fig. 4A could be improved. The superimposition of open and closed structures in panel A takes some time for the reader to grasp. Maybe showing structures side by side with key distance measurements highlighting regions where there is movement between open and closed states would help, and then showing superimposition for a more limited view of where PIP2 binds? In panels B and C, it is not easy to appreciate how the structure in the open state disrupts the binding of ATP to the inhibitory site. Perhaps some use of space-filling models like those in Fig. S6 would help to illuminate the space occupied by ATP in the closed state, along with a zoomed-in view of all the residues coordinating ATP, and also similar views for how the conformational change during opening would interfere with ATP binding or move key coordinating residues. Fig. 4 contains a lot of information but it is not presented in a way that is easy for the reader to comprehend.

We have revised this figure (revised Fig. 5) as suggested and hope it is now improved.

1. In the figures, the authors focus their comparisons between the structure solved in this manuscript (open, PIP2 bound) and previous structures solved in the same lab (closed, ATP and/or inhibitors bound). While comparisons are made in the text to the open and 'pre-open' structures solved by other investigators, it might be clearer if visual comparisons were offered as well – especially of the interaction between the SUR1-W51 residue and the wild-type Kir6.2-Q52 residue in both other structures, the similarity of which offers support for the authors arguments about common structural rearrangements on page 17.

We have added a supplement figure (Fig. S6) to make this comparison.

1. Could the authors comment on how the Rb efflux assay results in Fig. 6 panel D add to the electrophysiological results shown in that figure in panels B and C? Differences in data from the flux assay in Fig. 6D may reflect changes in channel function, but they may simply reflect different expression levels for mutant channels.

The Rb efflux data shown in the original Fig. 6 (now Fig. 7) complement the electrophysiology data and show channel behaviour in intact cells. For all mutants we confirmed comparable expression levels in transfected cells by Western blots.

1. The map in Fig. 7 corresponds to both loss-of-function mutations, that cause diabetes, and gain-of-function mutations, that cause hyperinsulinism. Is it the opinion of the authors that these mutations mediate their effects by modulating PIP2 binding? LOF mutations could reduce PIP2 binding whereas GOF mutations could strengthen PIP2 binding.

We believe the reviewers meant loss-of-function mutations that cause hyperinsulinism and gain-of-function mutations that cause neonatal diabetes. As stated in the Discussion section, these mutations could exert their effects by modulating PIP2 binding or by affecting PIP2 gating allosterically.

1. As referred to above, Fig. S6 in DOI:10.1073/pnas.2112267118 shows lipid densities near the new PIP2 site – how do they compare to the location of the PIP2 densities resolved in this manuscript?

Please see the comparison we have now included in the revised Fig.S4a, b.

1. The idea advanced in the discussion and Fig. S6 that PIP2 binds to the new site only after the channel opens is interesting and seems conceptually related to what was recently proposed for PIP2 modulation of KCNQ by Mandala and MacKinnon (PNAS 2023). It might be helpful for the reader to see those dots connected.

We thank the reviewers for the suggestion and have now cited the paper by Mandala and MacKinnon (page 10 top, reference 49).

1. The allosteric models of ligand regulation of the KATP channel have been predicated on the existence of four PIP2 binding sites across the molecule – how does the existence of eight potential PIP2 binding sites alter previous attempts to quantitively model KATP activity (e.g. reviewed in DOI:10.1085/jgp.200308878 and DOI:10.1085/jgp.201711978)? Perhaps this deserves a comment.

This is an interesting question that would be an excellent topic for researchers who are interested in kinetic modeling.

1. The experiments described on pages 13-14 and ion Fig. 6 that explore the Kir6.2-Q52 and SUR1-W51 interaction are convincing, but the dose-response curves (especially for WT and the W51C-Q52R) would benefit from some lower concentrations of ATP.

We have conducted additional experiments to obtain data at lower ATP concentrations (see revised Fig. 7).

(This is a response to peer review conducted by Biophysics Colab on version 1 of this preprint.)

Consolidated peer review report (5 September 2023)

GENERAL ASSESSMENT

KATP is a remarkably important potassium-selective ion channel that is inhibited by intracellular ATP, allowing it to serve key roles throughout the body, including regulation of insulin release from the pancreas. Driggers et al. describe an important study that reports the structure of an open KATP channel complex formed from the Q52R diabetes mutation of Kir 6.2, SUR1, and long-chain PIP2. Although earlier structures have been determined in closed, open and inactivated conformations, none have resolved where PIP2 binds. This has been an important limitation of the available structures given the key role of this membrane component in promoting the open state and influencing the inhibitory actions of intracellular ATP. The open channel structure reported here resembles a previous structure from the MacKinnon laboratory of a mutant channel that exhibits a very high open probability (G334D, C166S). The authors also show that channel opening is accompanied by a dilation of the Kir6.2 inner helix gate, in particular rotation of L164 and F168 away from the channel's pore, and by a conformational rearrangement at the interface between Kir6.2 and the TMD0 domain of SUR1.

The key advance that allowed the authors to resolve PIP2 bound to KATP appears to be the use of brain-derived long-chain PIP2, which was incubated with membranes prior to extraction of the channel protein with digitonin and purification, as well as the use of the Q52R mutant that promotes the open state. Remarkably, the structures of PIP2 bound to KATP reveals two PIP2 binding sites: one related to previously resolved sites in other Kir channels; and a new, unanticipated one where the lipid snuggles into the interface between Kir6.2 and the TMD0 helix of SUR1, a region of SUR1 previously implicated in promoting the open state of KATP. To examine the functional impact of the two PIP2 binding sites, the authors identify two positively-charged residues – one in each binding site – to neutralise by mutation to alanine, in an effort to disrupt the two putative PIP2 interactions. Indeed, they find that KATP channel currents on patch excision are very small and require much longer exposure to PIP2 to fully activate, compared to wild-type channels. Although one could question the physiological relevance of the new PIP2 binding site, that PIP2 remains bound throughout extraction and purification in digitonin solutions, and can be readily resolved in the structure, suggests that interactions of longer-chain PIP2 with both sites is quite favourable and likely to be occupied under biological conditions. One of the remarkable features of the new structures is that PIP2 binding to KATP causes a conformation change in the inhibitory ATP binding site, providing a mechanistic explanation for how PIP2 and ATP antagonistically engage to promote open or closed states, respectively. The structure also reveals how the Q52R mutant likely forms a cation-π interaction with W51 of SUR1, explaining how the diabetes mutation promotes the open state of KATP. Ultimately, further experiments will help unravel the physiological impact of the newly identified PIP2 site, as the electrophysiology presented in this structural study is understandably limited. However, that does not diminish the impact of the study.

Overall, this is an important study that helps to explain how PIP2 exerts such a profound regulatory influence over KATP, which will be valuable for future studies on KATP and of general interest to scientists investigating how PIP2 regulates other membrane proteins. The preprint is well-written, the work appears to have been carried out with rigor and attention to detail, and the authors present new conclusions and discuss them in the context of previous findings, some of which have been enigmatic until now.

RECOMMENDATIONS

Essential revisions:

1) Most of the figures focus on a comparison of the new PIP2-bound open state for the Q52R mutant with a closed state of KATP. A more extensive structural comparison between the PIP2-bound open structure and other open structures solved in absence of PIP2 (e.g. ref 27 where Kir6.2 mutations C166S and G334D were used) would help clarify the functional roles of the putative PIP2 binding sites. A structural comparison of the PIP2 binding sites between the two open structures (apo and holo) would reveal whether the PIP2 binding sites are conserved in the absence of PIP2, for example. Such a comparison would help the general reader to understand which of the structural changes observed in the new structure have been seen before and those that have not. Another example would be to clarify the extent to which structural changes around the inhibitory ATP binding site seen here are related to those in previous structures thought to be open.

2) It would be valuable for readers if the authors could explain their thinking about why the new PIP2 binding site is likely to be physiologically relevant. In its current form, some readers may be unconvinced about whether the new site is occupied under physiological conditions. For example, in the last paragraph of page 15, the authors acknowledge that in their previously published closed structures without exogenous PIP2, they saw lipid densities in the novel PIP2 site which they modelled as phosphatidylserines. Similar lipid densities were also seen near this site in the other published open state (see Fig. S6 in DOI:10.1073/pnas.2112267118). In the next paragraph on page 16, they also comment on the unusually low specificity of Kir6.2 towards phosphoinositides and other lipids, and the ability of purified KATP channels to open in the absence of PIP2. Given these findings, and the potentially high concentration of PIP2 incubated with the sample, is it conceivable that the new PIP2 site is not occupied under physiological conditions? What do the authors know about the molar fraction of PIP2 achieved in the final sample and how this might compare to the estimates of PIP2 abundance in native human cell membranes (0.2-1%)? Would PIP2 ever reach high enough concentrations in the membrane for this site to be bound? The authors might also emphasize that the channel was only exposed to brain PIP2 for a short time before being extracted and purified in the detergent solution, indicating that the interaction between PIP2 and the channel at both sites is quite strong and likely to be occupied physiologically.

3) The electrophysiological data presented in Fig. 2, while corroborating the existence of a second PIP2 site, is not definitive. On page 9 of the text, the authors mention striking differences between wild-type and mutant channels in terms of "the initial currents upon membrane excision, the extent of current increase upon PIP2 stimulation, and the PIP2 exposure time required for currents to reach maximum." The extent of current increase is shown for multiple patches in Fig. 2E and the other differences are inferred from representative traces. The authors may wish to include some form of quantification for the amount of initial current and time course for data from multiple patches. For example, the authors mention "barely detectable currents" for the SUR1-K134A/Kir6.2-R176A mutant. Taking into account the difference in scale bars, the currents in the example provided don't look any smaller than the currents from Kir6.2-R176A/SUR1 channels. Given the proximity between the two sites, it seems possible that a mutation in one site could allosterically affect PIP2 binding at the other site. In principle, two mutations could independently affect PIP2 binding at the same functional site and have additive effects. Perhaps the strongest arguments in favour of two distinct functional sites come from the mutation map in Fig. 7, which nicely matches the two bound PIP2 molecules, and previous studies showing that KATP is less sensitive to PIP2 in the absence of SUR1, which forms part of the second binding site.

4) The increase in current in PIP2 in Fig. 2E may represent the extent of the increase in probability of opening. However, calculating the fold increase in current depends on accurate measurements of the very small currents at the beginning of the experiment, which will be heavily affected by residual leak or noise. In the absence of any direct measurements of open probability (for example with single channels), the authors may wish to discuss these limitations in the text.

Optional suggestions:

1) The Kir6.2-Q52R mutation, which stabilizes the open channel, mediates its effects by interacting with W51 on SUR1 (Fig. 6). Q52R is also very close to the PIP2 headgroup in the novel binding site and thus could help stabilize PIP2. Hence, it would be interesting to test the PIP2 sensitivity of this mutant in excised patches, as in Fig. 2D,E. If PIP2 binding at the second site is favoured by the mutation, the PIP2-induced increase of KATP current should be lower than that observed in WT channels.

2) It would be helpful for the authors to provide a biochemical interpretation for the functional results in Fig. 2 D, E. It would seem that the two mutations, Kir6.2-H176A and SUR1-K134A, diminish PIP2 binding affinity but do not prevent PIP2 binding, as the low basal currents seen in the mutants can be rescued by increasing PIP2 concentration.

3) The discussion on the role of H175 on pH regulation is interesting, but speculative. As the H175K mutant still undergoes acid-induced inhibition (ref 39), it does not seem appropriate to state that the H175K mutant "abolishes channel sensitivity to pH" (p7). A positive charge at position H175 increases basal activity, suggesting that the cationic form of H175 mediates acid-induced activation. The structure shows two H175 rotamers but does not clarify which of these rotamers are populated at different pH values. In addition, there is no evidence to suggest that the cationic form of H175 preferentially interacts with PIP2 and that its neutral form interacts with E179 (p8). On the contrary, it seems more logical to predict that the cationic form of H175, which is positively charged, interacts with E179, which is negatively charged. It would be helpful to clarify several of these points.

4)There are many questions that come to mind that might be interesting topics to add to the discussion. What is the relative affinity of this novel site for PIP2 over other PI's and even other lipids? Given that previous attempts to establish this (e.g. cited in reference 38) may have been measuring the summed contribution of both sites, if both are functionally relevant (as the present results suggest), do the sites differ in their selectivity? Could this be a lipid binding pocket, which has been displaced by high levels of PIP2 and a locked-open channel? These are not trivial questions to answer, but they are important for understanding the relative importance of the two PIP2 binding sites for the function of KATP and it would be useful to discuss the limits of what can be reasonably concluded at this time. Some of these points might be addressed in the results while other could add to the discussion. In thinking about the roles of the two PIP2 binding sites, have the authors considered the possibility that the PIP2 site found in other Kir channels might act as a reservoir for PIP2 and that PIP2 moves to the new site at the interface with SUR1 once the channel opens?

5) Page 9, lines 6-10: The authors suggest that the slower washout of long-chain PIP2 activation from excised patches compared to that of short-chain synthetic PIP2 is due to hydrophobic interactions between the longer acyl chains and KATP. However, this observation has been previously explained by the differences in the solubility of short- and long-chain PIP2 and therefore their rate of partition into and out of the plasma membrane. Is any data available to distinguish these possibilities?

6) Can the authors provide higher quality micrographs in Fig. S1 along with a scale bar. Why are three different micrographs shown? Also, this figure would probably benefit from moving some of the text embedded in the figure to a traditional legend along with a somewhat expanded description of what is shown graphically in the figure.

7) In the main text when describing the results in Fig. 2D, it would be helpful for the general reader to first explain the protocol employing both low and high ATP concentrations and what value this has for assessing the impact of mutations. As it currently stands, the reader is left guessing why this expertly devised protocol was used.

8) In Fig. 3 it would be helpful to align the three panels so the reader can appreciate how the structure gives rise to the pore radius plot in panel C. Also, the point made about the G-loop not changing appreciably between closed and opens states would be good to show in the structures.

9) The G-loop was previously proposed to aid in preventing the leakage of K ions into the internal solution as polyamines block Kir channels (Xu et al, 2009 NSMB). It might be worth commenting on this as it seems compatible with what is found here in that region.

10) Fig. 4A could be improved. The superimposition of open and closed structures in panel A takes some time for the reader to grasp. Maybe showing structures side by side with key distance measurements highlighting regions where there is movement between open and closed states would help, and then showing superimposition for a more limited view of where PIP2 binds? In panels B and C, it is not easy to appreciate how the structure in the open state disrupts the binding of ATP to the inhibitory site. Perhaps some use of space-filling models like those in Fig. S6 would help to illuminate the space occupied by ATP in the closed state, along with a zoomed-in view of all the residues coordinating ATP, and also similar views for how the conformational change during opening would interfere with ATP binding or move key coordinating residues. Fig. 4 contains a lot of information but it is not presented in a way that is easy for the reader to comprehend.

11) In the figures, the authors focus their comparisons between the structure solved in this manuscript (open, PIP2 bound) and previous structures solved in the same lab (closed, ATP and/or inhibitors bound). While comparisons are made in the text to the open and 'pre-open' structures solved by other investigators, it might be clearer if visual comparisons were offered as well – especially of the interaction between the SUR1-W51 residue and the wild-type Kir6.2-Q52 residue in both other structures, the similarity of which offers support for the authors arguments about common structural rearrangements on page 17.

12) Could the authors comment on how the Rb efflux assay results in Fig. 6 panel D add to the electrophysiological results shown in that figure in panels B and C? Differences in data from the flux assay in Fig. 6D may reflect changes in channel function, but they may simply reflect different expression levels for mutant channels.

13) The map in Fig. 7 corresponds to both loss-of-function mutations, that cause diabetes, and gain-of-function mutations, that cause hyperinsulinism. Is it the opinion of the authors that these mutations mediate their effects by modulating PIP2 binding? LOF mutations could reduce PIP2 binding whereas GOF mutations could strengthen PIP2 binding.

14) As referred to above, Fig. S6 in DOI:10.1073/pnas.2112267118 shows lipid densities near the new PIP2 site – how do they compare to the location of the PIP2 densities resolved in this manuscript? Are the lipid densities present in Fig. S3C and D also compatible with PC?

15) The idea advanced in the discussion and Fig. S6 that PIP2 binds to the new site only after the channel opens is interesting and seems conceptually related to what was recently proposed for PIP2 modulation of KCNQ by Mandala and MacKinnon (PNAS 2023). It might be helpful for the reader to see those dots connected.

16) The allosteric models of ligand regulation of the KATP channel have been predicated on the existence of four PIP2 binding sites across the molecule – how does the existence of eight potential PIP2 binding sites alter previous attempts to quantitively model KATP activity (e.g. reviewed in DOI:10.1085/jgp.200308878 and DOI:10.1085/jgp.201711978)? Perhaps this deserves a comment.

17) The experiments described on pages 13-14 and ion Fig. 6 that explore the Kir6.2-Q52 and SUR1-W51 interaction are convincing, but the dose-response curves (especially for WT and the W51C-Q52R) would benefit from some lower concentrations of ATP.

REVIEWING TEAM

Reviewed by:

Surbhi Dhingra, Postdoctoral Fellow, NINDS, NIH, USA: structural biology (cryo-electron microscopy) and ion channel mechanisms

Jerome Lacroix, Associate Professor, Western University of Health Sciences: ion channel mechanisms, electrophysiology, fluorescence spectroscopy

Michael C. Puljung, Assistant Professor, Trinity College, Hartford, CT, USA: ion channel mechanisms, electrophysiology, fluorescence spectroscopy

Xiaofeng Tan, Research Fellow, NINDS, NIH, USA: structural biology (X-ray crystallography and cryo-electron microscopy) and ion channel mechanisms

Samuel Usher, Postdoctoral Fellow, University of Copenhagen, Denmark: ion channel mechanisms, electrophysiology

Kenton J. Swartz, Senior Investigator, NINDS, NIH, USA: ion channel structure and mechanisms, chemical biology and biophysics, electrophysiology and fluorescence spectroscopy

Curated by:

Kenton J. Swartz, Senior Investigator, NINDS, NIH, USA

(This consolidated report is a result of peer review conducted by Biophysics Colab on version 1 of this preprint. Comments concerning minor and presentational issues have been omitted for brevity.)

Consolidated peer review report (28 September 2023)

GENERAL ASSESSMENT

Ionotropic glutamate receptors mediate the large majority of excitatory synaptic transmission in the brain. These receptors consist of four classes: AMPA, kainate, NMDA and delta receptors. NMDA receptors are obligate tetramers composed of two GluN1 and two GluN2 (or GluN3) subunits. Compared to other iGluRs, they have the particularity of requiring two different agonists for their channel to open: glycine binding on GluN1 and glutamate on GluN2.

Seljeset et al. investigate the molecular determinants controlling ligand potency and NMDAR activity at the level of the ligand-binding domains (LBDs), where the agonists bind. They identify a specific position, D732, whose mutation to either leucine or phenylalanine leads to a constitutively active GluN1 subunit, and thus to NMDARs activated solely by glutamate. This aspartate is well known in the field, since it is a highly conserved, signature residue in iGluRs that binds amino acid ligands, together with an arginine in the LBD upper lobe. Surprisingly, although glycine cannot further activate GluN1-D732L/GluN2Awt receptors, glycine site antagonists like 5,7-DCKA or CGP-78608 can still bind and inhibit NMDAR activity. This study is therefore very intriguing, as it raises new questions about something that was previously thought to be understood. By using a combination of unnatural amino acids and conventional mutagenesis, the authors propose that D732 contributes to glycine-mediated effects by changing local interactions with nearby residues. In addition, they show that this behavior is specific for the GluN1 subunit, since mutation of the equivalent aspartate in the GluN2 subunit does not yield constitutively activated GluN2 subunits. Finally, the authors identify a homomeric iGluR from the placozoan Trichoplax adhaerens, Trichoplax AKDF19383, in which this conserved aspartate is replaced by a tyrosine. When expressed in Xenopus oocytes, the channel shows constitutive activity. Mutation of the tyrosine into an aspartate, to convert Trichoplax AKDF19383 into a "classical" iGluR, decreases Trichoplax AKDF19383 constitutive current and allows this channel to be activated by glycine and D-serine. Interestingly, an adjacent residue that is a serine in most mammalian subunits is also a tyrosine in Trichoplax AKDF19383, and mutation of both tyrosines yields a glutamate-gated ion channel comparable to mammalian receptors. All of this suggests that the nature of the residue at position 732 influences not only ligand binding but also channel gating.

The study is technically sound, with appropriate controls, and uncovers intriguing properties of a position in GluN1 LBD at which specific side chain mutations can lock the subunit in an active state. Investigation of Trichoplast iGluR further reinforces these findings. This study should lead to a better understanding of how LBDs prime channel opening in iGluRs in the absence of agonists. In addition, co-agonist insensitive GluN1-D732L containing NMDARs could be used as tools to investigate the physiological consequences of NMDAR regulation by their co-agonist site. In contrast to previously engineered NMDARs activated solely by glutamate, which rely on the LBD being locked in its active state by cysteine bridges (Blanke and VanDongen, J Biol Chem 2008), GluN1-D37L/GluN2A NMDARs remain druggable (i.e. they can still be inhibited by glycine-site competitive antagonists). This is a great advantage when investigating the function of these receptors in a native context. The study identifies a few gaps that remain in our mechanistic understanding of D732's role in channel gating.Particularly, it is unclear how subtle modification of residue side chains at position D732 lead to such drastic changes in function and why these effects are specific to GluN1 LBD. Also, why does mutation of D732 into isoleucine lead to a constitutively active GluN1 subunit, while mutation of a closely related leucine residue prevents activation of the receptor by glycine? The idea of a "hydrophobic plug" formed by D732L or D732F sidechains leading to constitutive activation would benefit from further validation since other hydrophobic substitutions (A, V, I, Y, and W) do not produce similar effects. Finally, it would be interesting to carry out further investigations of the role of the interaction between D732 and Q536 in open conformation stability. Thus, this paper puts forth interesting questions that could be addressed by future studies, for example molecular dynamics simulations and exploration of the LBD free energy landscapes (as in Yao et al., Structure 2013), to understand the impact of the GluN1-D732L mutation on GluN1 LBD conformational mobility.

RECOMMENDATIONS

Essential revisions:

1. Page 2, "These data show that essentially all substitutions at the GluN1-732 position decrease glycine potency, but leucine and phenylalanine substitutions also remove the requirement for glycine co-agonism in GluN1/GluN2A NMDA receptors": One other hypothesis for the lack of glycine dependence of GluN1-D732I and D732Y + GluN2A receptors could be that the mutated receptors have a glycine potency so high that GluN1 LBD is already saturated by contaminating, ambient glycine. At this point in the paper, the authors cannot distinguish between one hypothesis or the other, therefore we suggest that this sentence be rephrased. Later in the text, control experiments with GluN1-R523K mutations that kill glycine binding and competition with 5,7-DCKA show that glycine-independent activation of GluN1-D732L/GluN2A mutants is not due to constitutive occupancy of GluN1 LBD by contaminating glycine.
2. Does glycine insensitivity in GluN1-D732L/GluN2A NMDARs reflect a constitutively active GluN1 subunit or is this subunit locked in another conformational state that cannot be further modified by glycine? This could be answered by estimating the maximum open probability of GluN1-D732L/GluN2A NMDARs compared to their wt counterparts. To estimate Po, the authors could measure the kinetics of NMDA receptor current inhibition by MK801 (the slower MK801 inhibition, the lower the Po; see Chen et al., J. Neurosci 1999; Blanke and VanDongen, JBC 2008) in the presence of saturating agonist concentrations (100 μM Glu, 100 μM Gly for wt and only 100 μM Glu for mutant).
3. Page 4: The term "hydrophobic plug" is not fully justified since other hydrophobic residues do not lock GluN1 LBD in its active state.
4. Figure 2, redox sensitivity of GluN1-D732L/GluN2Awt: It would be helpful to explain the point of this experiment – maybe to investigate if the D732L mutation has an impact on the receptor gate rather than on the LBD? In any case, the authors should investigate the effect of DTT on the activity of wt GluN1/GluN2A receptors to determine whether there is an absence of an effect of the D732L mutant on redox sensitivity.
5. Page 6: The authors find that mutation of Q536 decreases glycine potency and conclude there is an interaction between D732 and Q536. However, the effects of D732 and Q536 mutations could be independent, therefore the authors should consider mutating both residues together to look at the additive/non-additive effects of the mutations. Or perhaps, note in the Discussion that some sort of mutant cycle analysis or molecular dynamics simulation would be needed to rigorously test these ideas.
6. Page 6, "A hydrophobic plug does not cause constitutive activity in all NMDA receptor subtypes": This title is misleading as it raises the expectation that the effect of GluN1-D732L has been investigated in the context of GluN1/GluN2A, GluN1/GluN2B, etc NMDARs. Instead, the equivalent mutation is made in the GluN2 subunit. We suggest using the word "subunit" rather than "subtype".
7. Page 7, effect of GluN1-D732L in the context of GluN1/GluN3 NMDARs: We would not expect current to be observed with GluN1-D732L/GluN3 NMDARs, since locking GluN1 LBD in its active state desensitizes the receptors. The effect of the D732L mutation seems therefore conserved between GluN1/GluN2 and GluN1/GluN3 NMDARs. In addition, when using CGP, please cite Grand et al., Nat. Commun. 2018 since they were the first to use CGP as a tool to record GluN1/GluN3 currents.
8. Figure 5C: It is stated in the text that the aspartate position is "highly" conserved. However, no actual number or percentages are given for this statement. How does it compare to the residues in the highly conserved SYTANLAAF motif or other conserved positions? This sort of analysis does not need to be done for the entire receptor, but perhaps for glycine and glutamate binding residues and SYTANLAAF motif, to give a quantitative feel for statements about conservation. In addition, what other types of residues occupy this position in other species? And what was the number of species/subunits included in the analysis?
9. Figure 5, panel F: From what we understand, the authors created dose-response curves for wt Trichoplast AKDF193863 based on steady-state currents and for Y742D/Y743S mutants based on peak currents. If this is the case, one cannot compare the two dose-response curves since peak current potentiation and steady-state inhibition likely reflect different conformational transitions.

Optional suggestions:

1. Figure 2, glycine/DCKA competition: It is difficult to understand how a GluN1 LBD-locked closed (active state) could still bind DCKA. If the open-to-close equilibrium of GluN1 LBD is displaced towards its closed state, then DCKA Ki should be shifted to the right compared to wt receptors. Additionally, DCKA inhibition kinetics should be slower if DCKA needs to "wait" for rare resting-like conformational changes to bind. Did the authors investigate DCKA potency and inhibition kinetics?
2. The authors show in many panels that GluN1/GluN2A currents desensitize (e.g. Fig.1B, 3C, 4A). In Xenopus oocytes, NMDAR currents do not normally desensitize. We fear this desensitization might stem from contamination of the NMDA current by calcium-activated chloride channels, which can be activated by high quantities of barium when large NMDAR currents are measured. To avoid this problem, we advise that NMDA currents above 2 µA are avoided.
3. Page 5, investigation of D732 state-dependent interactions: Mutation of residues near D732 to unnatural amino acids to replace the peptidic NH do not bring much information about the mechanisms of D732 action. The fact that the 734Aah and 735Vah cannot mimic the effect of the D732L mutation could be due to many factors, including the fact that changing the peptide bond probably changes the local structure of the LBD. Perhaps mention this in the discussion.
4. It is intriguing that the D732L mutation locks an active conformation of the GluN1 subunit but not the GluN2 subunit, suggesting two different mechanisms of LBD closure by glutamate and glycine. It would be interesting to look at the effect of the equivalent mutation on the GluN3 subunit to investigate if this locking effect is specific to glycine-binding LBDs or just to the GluN1 subunit.
5. Page 9: Discussing the position of residue side chains from structures with 4 Å resolution does not seem relevant and would benefit from a caveat.
6. Page 10: We don't understand the point that the authors want to make with the activation of Aplysia californica. Please clarify.
7. In iGluRs, constitutive currents are often induced by mutations in the gate region, near the SYTANLAAF motif (e.g. lurcher mutations). Does the sequence around the gate of Trichoplast AKDF193863 predict channel constitutive activity?
8. D-serine is another co-agonist that binds the GluN1 subunit. Compared to glycine, D-serine can make additional interactions with the lower lobe of GluN1 LBD. It would be interesting to look at D-serine dose-response curves in GluN1-D732L/GluN2A receptors: are these receptors also D-serine insensitive or can they be further activated by D-serine?

REVIEWING TEAM

Reviewed by:

Sudha Chakrapani, Professor, Case Western Reserve University, USA: Structure, function and modulation of neurotransmitter receptors

Laetitia Mony, Permanent Researcher, Institute of Biology of École Normale Supérieure, France: NMDA receptor structure-function relationships and pharmacology

Lonnie Wollmuth, Professor, Stony Brook University, USA: NMDA receptor structure-function relationships and pharmacology

Curated by:

Sudha Chakrapani, Professor, Case Western Reserve University, USA

Evaluation statement (1 September 2023)

Flores-Aldama and colleagues set out to identify molecular determinants of fast inactivation in the TRPV6 ion channel, a mechanism not observed in the closely related TRPV5 channel. The work focuses on a helix-loop-helix (HLH) motif, located at the interface between several important regions for channel gating. Using molecular dynamics simulations and analysis of mutations, the authors identify pairs of amino acid residues in a structural triad formed by the HLH, S2-S3 linker, and transmembrane domains, which show different conformations in the available TRPV5 and TRPV6 cryo-EM structures. An important aspect of the study is that some of the structural hypotheses were derived from an evolutionary analysis of sequences from orthologues of both channels, demonstrating the value of this type of analysis.

Biophysics Colab considers this to be a convincing study and recommends it to scientists interested in the molecular determinants of ion channel gating.

(This evaluation by Biophysics Colab refers to the version of record for this work, which is linked to and has been revised from the original preprint following peer review.)

Evaluation statement (24 May 2023)

Yang et al. present valuable information about ligand interactions with the serotonin transporter SERT, innovatively purified from pig brain using Fab fragments. The approach of using natively expressed SERT is notable for its potential insight into binding of endogenous membrane components such as lipids. Data distinguishing binding of the psychostimulants methamphetamine and cocaine add to our knowledge of substrate and inhibitor interactions with SERT and allow direct comparison with the closely related dopamine transporter DAT. The authors carefully state the limitations of their findings, including the possibility that the monomeric transporter stable in detergent micelles might exist in a multimeric state in native membranes.

Biophysics Colab considers this to be a convincing study and recommends it to scientists interested in the structure, mechanism and ligand interactions of neurotransmitter transporters.

(This evaluation by Biophysics Colab refers to version 2 of this preprint, which has been revised in response to peer review of version 1.)

Authors' response (23 March 2023)

GENERAL ASSESSMENT

Yang et al. present valuable insight about ligand interaction with SERT. It is notable for the use of endogenously expressed SERT from pig brain, rather than from a heterologous expression system, and the value of using Fab fragments that as a tool for detecting and purifying SERT. The use of natively expressed SERT allows insight into binding sites for endogenous membrane components, including lipids, that copurify with the transporter. Data on binding of the psychostimulants methamphetamine and cocaine to the purified protein also adds to our knowledge of substrate and inhibitor interactions with SERT.

In general, we liked the manuscript but have some suggestions for improvement and clarification. There was unanimous agreement that the conclusions regarding SERT oligomerization were stated in a way that many readers would mis-interpret. Although the manuscript states that the result of the study do not exclude SERT oligomerization in its native environment, that statement is not reflected in the abstract and is downplayed in the discussion. The discussion clearly points out why some previous proposals for SERT oligomerization may conflict with our knowledge of SERT structure and function. However, it is also clear that the extraction of SERT using DDM, although it's influence on SERT structure may be mild, can remove other membrane components that are required for oligomer stability.

We have qualified our statements related to SERT oligomerization to make it clear that we are studying SERT extracted using a mild non ionic detergent and, in the membrane and in the presence of specific lipids, the oligomerization state of SERT might be different.

A second issue raised by the reviewers concerns the poses of bound ligands and their effect on conformation. There is an expectation that substrate binding converts NSS transporters like SERT to a more inward-facing conformational ensemble while some inhibitors (particularly cocaine in the case of SERT) have the opposite effect. Statements in the manuscript that METH stabilizes an outward-open conformation while cocaine stabilizes an occluded state seem to contradict this expectation. A close reading of the results, and examination of the structures, indicates that the backbone of SERT is outward-open in both cases and that the orientation of Phe372 occludes cocaine but not METH. Thick and thin gates have already been defined for LeuT so the implication that orientation of Phe372 represents an additional gating process may confuse readers.

We have rephrased our description of the conformations of the SERT-ligand complexes such that they are in better alignment with previous descriptions of transporter conformations and the nature of the gates.

The observation that METH does not stabilize a less-outward-open conformation may result from its lower affinity for SERT and one wonders why a more SERT-selective amphetamine derivative such as MDMA or p-chloroamphetamine was not used. Was the objective to compare the binding pose and conformational response of SERT to that of dDAT with the same ligands?

Yes, we carried out studies on pSERT to allow the most 'parallel' comparisons with the previously studied dDAT complexes.

A third issue is the designation of SERT purified from pig brain as nSERT rather than "native porcine SERT" (pSERT or ssSERT for Sus scrofa). One wouldn't use nSERT to define SERT extracted from Drosophila or C. Elegans by the same technique.

We have defined the transporter as pSERT in the revised version of the manuscript.

RECOMMENDATIONS

Revisions essential for endorsement by Biophysics Colab:

1. Clearly indicate that the lack of oligomer detection in detergent-solubilized SERT is not evidence against SERT oligomerization in situ, and that detergent can disrupt interactions required for oligomerization, thereby biasing the oligomeric status of SERT. Also, use an alternative for DDM-solubilized SERT other than "native" or "nSERT"

See above

1. Distinguish between the local occlusion of cocaine by reorientation of the Phe-372 side chain and the occluded conformational state of SERT that involves movement of TMs 1 and 6 towards TMs 8 and 10. Also explain the choice of METH rather than an amphetamine derivative more selective for SERT. Do the structures explain the difference in METH affinity between SERT and dDAT?

Also see above

1. Because neither the DHA density nor the MD simulations provide an unambiguous identification of DHA, designation of this density as DHA should be clearly stated as provisional.

We have repeated the MD simulations, also exploring occupancy of the allosteric site by DDM, and find that DDM is preferred over DHA. We have 'toned down' our suggestions that DHA might occupy the site accordingly.

Additional suggestions for the authors to consider:

1. Does DHA fulfill a functional role? The carboxyl group is close to Arg141, which can form an ion pair with Glu531 to close the extracellular pathway. Is there any indication that DHA could interfere with this process, and alter SERT activity?
2. Is there sufficient purified material to perform a lipidomic analysis and to confirm the identity of DHA at the allosteric site?
3. Would incubation of the membranes with METH or cocaine prior to detergent extraction affect the composition of associated lipids?
4. PIP2 has been proposed to promote SERT association in vivo. Is it possible that PIP2 addition would change the oligomeric nature of DDM-extracted SERT?
5. We suggest trying to polish the final particle stack of both data sets further. Have the authors tried to separately refine the 3D classes from Relion, and not to combine them? Alternatively, one could perform an additional round(s) of heterogenous refinement on the final particle stack, and a final nonuniform refinement. There seems to be an opportunity to improve the quality of maps by further polishing the particles.

(This is a response to peer review conducted by Biophysics Colab on version 1 of this preprint.)

Evaluation statement (22 August 2023)

Bansal et al. present an atomistic view of the transition cascade of the class F GPCR Smoothened (Smo). The extensive long-range molecular dynamics simulations together with stochastic modelling provide theoretical insight into Smo activation and how this is modulated by different ligands. The work identifies testable hypotheses for functional studies of Smo and other class F GPCRs. Future simulations of regions beyond the seven-transmembrane bundle, particularly the cysteine-rich domain, will afford a more complete understanding of receptor activation.

Biophysics Colab considers this to be a convincing computational study and recommends it to scientists interested in the conformational dynamics of class F GPCRs.

(This evaluation by Biophysics Colab refers to version 2 of this preprint, which has been revised in response to peer review of version 1.)

Evaluation statement (16 June 2023)

Maria-Solano and Choi present the dynamics underlying allostery of the adenosine A1 receptor, providing valuable insights into the receptor's activation pathway. The enhanced sampling molecular dynamics simulations of available structural data, followed by network analysis, reveal transient conformational states and communication between functional regions. The authors carefully state the limitations of their work, including the restricted convergence of the free energy landscape and missing water-mediated hydrogen bond coordination. Collectively, the findings provide a convincing framework to advance rational design strategies of specific modulators with desired modes of action.

Biophysics Colab considers this to be a convincing study and recommends it to scientists interested in the structural dynamics, allosteric pathway activations, and free energy landscapes of GPCRs.

(This evaluation by Biophysics Colab refers to version 5 of this preprint, which has been revised in response to peer review of versions 3 and 4.)

Authors' Response (2 June 2023)

GENERAL ASSESSMENT

The objectives of the study: This paper aims to characterize the dynamics that drive allostery of the adenosine A1 receptor (A1R) via computational analysis of its activation free energy landscape and measurements of the appropriate geometrical parameters. This is done by focusing on the allosteric signaling pathways in different activation states, from inactive to active states via intermediate and pre-active ones, as well as the characterization of putative drug-binding pockets. The long-term objectives are to eventually be able to aid drug discovery efforts for this therapeutically important GPCR.

Key findings and major conclusions: Conventional MD does not enable the sampling of the complete conformational landscape of receptor activation. Instead, enhanced sampling MD simulations are required to achieve this. Using metadynamics, the authors decipher the activation pathway of A1R, decode the allosteric networks and identify transient pockets. The protein energy networks computed throughout the inactive, intermediate active, pre-active and active conformational states unravel the extra and intracellular allosteric centers and the communication pathways that couple them, whereby the pathways are reinforced in the activated state. These conformations primarily differ in the dynamics of the ionic lock motif that couples TM3 to TM6 in the inactive conformation and reveal that G-proteins are required to fully stabilize the active conformation. Support for these findings comes from prior mutagenesis work on the A1R that identified key allosteric residues that in many cases map to identified communication nodes. Finally, the authors identified allosteric pockets throughout the A1R in four different conformational states that support prior experimental and MD studies on the mechanism of the positive allosteric modulator MIPS521 and which could be targeted for the design of modulators. Overall, these findings provide complementary support to a structure-based mechanism of activation and allosteric modulation of A1R, and extend the findings to incorporate dynamics across the full activation pathway.

The perceived strengths and weaknesses: This preprint employs a combination of computational techniques to successfully reconstruct and analyze the conformational ensemble of the A1R activation. The metadynamics simulations supported the aim of the study, the results are clearly presented and the work is very well written. The authors could improve the discussion of how the protein energy network analysis could further advance rational design of specific modulators with a desired mode of action. The computational approach needs to be refined to be robust, with a focus on characterizing the convergence of the free energy landscapes. Overall, A1R is a good choice as the target for this study as there is existing structural and pharmacological data to support preliminary findings. Moreover, the framework presented herein could be adapted and scaled to other GPCRs with structural templates, which might enable comparison of allosteric pathways across families and classes.

We thank the reviewers for contextualizing the findings of this study and for highlighting that our work provides complementary support to the mechanism of activation and allosteric modulation of A1R. We also thank the reviewers for their comments and suggestions, which had a great contribution to improve the quality and significance of the revised version of the preprint.

RECOMMENDATIONS

Revisions essential for endorsement:

1. The paper could better demonstrate how the insights gained herein will or could lead to progress in the rational design of specific modulators with a desired effect. The authors should outline and discuss how they envision the modeling pipeline they have designed will be used towards this goal and tone-down or explain why "this information is essential to ease the design of allosteric modulators for A1R.". A recent study on FFAR1, where the authors targeted a specific dynamic pocket could be helpful in this respect (https://www.pnas.org/doi/full/10.1073/pnas.1811066116). Specifically, this might entail: How does specificity for a receptor correlate with pockets forming in a specific state? From this, how does one design an agonist vs. an antagonist vs. an inverse agonist? Does breaking a specific network select a function of the drug? How would another group follow up on this work, for example in a virtual screening campaign?

We agree with the reviewers that a more comprehensive discussion of the points they mention is highly relevant to the study. Firstly, we have rephrased the last sentence of the abstract as "This information can be useful to ease the design of allosteric modulators for A1R" to ensure the significance of our results is not overstated. However, to address the reviewer's feedback more thoroughly, we conducted additional simulations with a positive allosteric modulator (MIPS51) and added an additional sub-section in the results, which includes three new figures (Figure 7-8 and S12):

"ADO and MIPS51 PAM have a significant impact on the energy networks. In order to establish a connection between the energy networks and the mode of action of allosteric modulators, we focus on exploring the effect of MIPS521 positive allosteric modulator (PAM) and ADO agonist as a proof of concept. Experimental assays and Gaussian accelerated MD determined that MIPS521 PAM increases the binding affinity of ADO in the orthosteric site.[19] Thus, PB and PD must be allosterically coupled. Among MIPS521 PAM pocket residues, only L2426.43, L2456.46, S2466.47 and G2797.44 were experimentally found to affect the PAM cooperativity (Figure S11). Interestingly, the PEN obtained in presence of ADO captures these key residues along activation, including TM6 (L2426.43 and L2456.46) in the intermediate, L2426.43 and S2466.47 in the pre-active and L2426.43 and TM7(G2797.44) allosteric residues in the fully-active ensemble (Figure 7). Indeed, G2797.44 becomes a key node in the PEN of the fully-active ensemble. This evidence suggests that although both PD and PB are open in all conformational states, their energy coupling is particularly stronger during the receptor activation.

This prompted us to investigate whether the binding of ADO and the MIPS521 PAM can affect the allosteric communication between PB and PD sites. To that end, we performed cMD of the heterotrimeric Gi2 protein ADO-A1R-Gi2 complex in presence of the PAM (PAM-ADO-A1R-Gi2 complex) and in absence of adenosine (A1R-Gi2 complex) in order to compute their conformational landscape and energy networks following the same protocol for the ADO-A1R-Gi2 complex (Figure 8 and S12). The analysis of the PEN of A1R-Gi2 complex reveals that in the absence ADO, the receptor displays a reduced allosteric communication between PB and functional regions of the receptor, such as the extracellular allosteric center, TM6 and PD allosteric site. As expected, the presence of ADO restores the allosteric coupling between PB and TM6, which could explain the increase of receptor activity associated with agonist binding. Additionally, our analysis of the PAM-ADO-A1R-Gi2 complex shows that the PAM reinforces the TM7-ECL3-ECL2 allosteric pathway that couple PD with PB, and ECL2 now communicates to the intracellular region through TM5 (Figure 8). Notably, a recently published study reported that the orhosteric pocket contracts after ADO binding, as demonstrated by shortened distances of the so-called vestibular lid (defined as the sum of length of the triangle perimeters formed by E17045.51-Y2717.36-E17245.53 interacting residues) and the E17245.53-K26567 salt bridge.[48] Remarkably, the TM7-ECL3-ECL2 enhanced pathway by PAM effect contains the vestibular lid and the E17245.53-K26567 salt bridge residues (Figure 8). This suggest that PAM promotes the contraction of PB, leading to the stabilization of the ADO-bound state. Thus, the enhanced energy coupling between PB and PD may be responsible for the increase in the binding affinity of ADO in presence of the PAM, as observed experimentally.[19] This data indicates that allosteric modulators are able to enhance and redistribute the energy networks, which is likely attributed for their effects on the receptor activity."

The new insights gained from our additional simulations have significantly enriched the discussion on how the protein energy network analysis can contribute to the rational design of specific modulators with desired modes of action. In light of these finding, the last paragraph of the discussion has been rephrased as:

"As a proof of concept, we focus on the PD, which corresponds to the binding site of MIPS52, a positive allosteric modulator (PAM) that increases Adenosine binding affinity in the orthosteric site (PB). Although PD is open in all conformational states the communication between PB and PD is enhanced along activation capturing the allosteric residues that were found to affect its PAM from the intermediate to the fully active. Based on this observation, we hypothesize that drugs that bind pockets and interact with PEN residues, which progresses towards regions of the receptor where function can be altered, may potentially affect the receptor activity through allosteric effects. Additionally, the pocket where the drug binds must be open at least in the conformation state that is targeted. As a practical aspect, virtual screening campaigns could use this information during the design procedure by selecting drug candidates that perform stronger interactions with the PEN contained in the pockets.

To further support this hypothesis, we explored the allosteric effects of ADO and MIPS52 PAM on the PEN. Interestingly, we observed that ADO is crucial for the formation of the extracellular center and its connection with TM6 pathway. Furthermore, MIPS52 PAM reinforces the pathway that connects PB and PD pockets and redistribute other connections. These alterations in the PEN can be related with their mode of action. ADO may increase the activity of the receptor through its communication with TM6 and the PAM may increase ADO binding affinity though stronger energy coupling between PD and PB pockets. These findings imply that the mode of action of allosteric drugs could be predicted depending on how they redistribute the PEN."

Accordingly, the last paragraph of the conclusions has been rephrased as:

"As a proof of concept, Adenosine and a previously experimentally determined positive allosteric modulator were found to enhance and redistribute the energy networks of the receptor in a manner that is consistent with their respective functions. The prediction of drug effects depending on how they redistribute the protein energy networks presents a promising avenue for drug discovery. All these system-specific structural dynamics understanding provides useful information to advance the design of A1R allosteric modulators on the basis of structure-based drug design. This computational approach can be also transferable to other GPCRs and related receptors, which is of interest for the design of novel allosteric drugs."

1. Free energy calculations:

a. A proof of convergence of the free energy calculations is missing. The authors argue that obtaining landscapes that do not change over time is proof of convergence, but this is incorrect in well-tempered metadynamics. The fact that the heights of the Gaussians decrease over time guarantees that the landscape will be stable over time, and the way to check convergence is to show that the collective variables become diffusive after convergence. In addition, to validate that the choice of collective variables (CV) is actually appropriate, they should check that CVs that were not biased are also diffusive. This would be best studied by looking at the behavior of microswitches that were not considered, such as ones describing the PIF motif, the NPxxY motif, the ligand binding pose, etc.

The goal of the well-tempered approach [Phys. Rev. Lett. 2008, 100, 020603] is to improve the convergence of the energy landscapes. This is achieved by gradually decreasing the height of gaussians over simulation. In this fashion, the height of the Gaussians is proportional to a decaying exponential function of the potential deposited in the currently visited point of the CV space. This technique has the added benefit of constraining reconstruction to the region of interest, reducing the risk of irreversible movement towards physically irrelevant regions of the CV space. As noted in the plumed tutorial (https://www.plumed.org/doc-v2.7/user-doc/html/master-_i_s_d_d-2.html), the fact that the Gaussian height is gradually decreasing should not be used as a measure of convergence. Rather, convergence can be assessed by monitoring the energy differences between chosen regions of the energy landscape over time (e.g. the inactive, intermediate and pre-active local energy minima used in our work). If this energy differences do not change significantly as a function of time, this can be taken as an indicator of convergence. We also would like to emphasize that our aim is to recover the major conformational states involved in the pathway of receptor activation rather than the study of subtle energy barriers and relative stability differences of the energy minima upon system perturbations. This objective has been made clear in the text.

We agree with the reviewers' comment that our measure of the convergence could be strengthened by additional analysis that verify the computed conformational pathway of receptor activation.

As suggested by the reviewers, we have plotted the CV1 values over time to asses convergence of our simulations (Figure S4). However, it should be noted that in this study, we have employed the walkers approach [J. Phys. Chem. B 2006, 110, 3533], which utilizes 10 replicas (walkers) to parallelize free energy reconstruction. Each walker simultaneously reconstructs the energy landscape by reading the Gaussian potentials deposited by the other walkers. Consequently, the correct time to stop the metadynamics simulation using the walkers approach becomes more problematic. To facilitate efficient sampling of the CV space and achieve convergence more rapidly, we utilized a sampling strategy that involved starting the simulation with walkers that spanned the entire CV space of interest. In this context, the fact that the walkers do not become trapped in the initial CV space and are able explore and cross into regions occupied by other walkers may serve as a useful indicator of convergence. This assessment of the convergence has been implemented before for Tryptophan Synthase, in which the resulting energy landscapes were consistent with experimental data. [J. Am. Chem. Soc. 2019, 141, 13049] and [ACS Catal. 2021, 11, 13733]

We have added the following paragraph in the convergence section including Figure S4:

"We have also assessed convergence by analyzing the CV1 values over simulation time. Figure S4A shows that during the first 100ns, walkers primary oscillates around their initial CV1 values. Subsequently, at around 200 ns walkers exhibit a higher frequency of crossing into regions occupied by other walkers. This is further supported by the exploration of W1 and W10, as shown in Figure S4B. These two walkers initially start the landscape reconstruction at the opposite extremes of the CV space. At 120 ns, they are able to escape from their respective basins and approach each other, sampling similar CV values (at approximately 240 ns). At this point of the simulation, only these two walkers have covered the entire conformational space of activation. Subsequently, they tend to return to previously sampled CV space. The observation that walkers do not become trapped in their initial CVs region, but instead explore and cross into other regions suggests that our sampling strategy, which involved starting the simulations with walkers that spanned the entire CV space of interest, has facilitated the exploration of the relevant conformational space. Although we cannot guarantee full convergence of the free energy landscape under these conditions, we successfully reconstructed the major conformational states of the receptor activation at 250 ns."

Accordingly, in the results section we have replaced "After 250 ns of accumulated time the FEL was considered to be converged (see Figure S3 and S4)" by "After 250 ns of accumulated time, we successfully reconstructed the major conformational states of the FEL (see convergence assessment in Figure S3 and S4)."

To further verify the accuracy of the collected conformational landscape, we have conducted additional analysis, which include the following:

"As a complementary analysis, we conducted the reweighting of the metadynamics simulations[28] to determine the free energy as a function of previously identified A1R micro-switches (ionic-lock, PIF motif, water-lock and toggle switch). The fact that we capture the distinct energy barriers associated with unbiased micro-switches highlights the accuracy of the metadynamics simulations in reproducing the pathway of activation and provides useful information to guide the selection of collective variables for future GPCR landscape calculations (Figure S5, S6 and S7)."

b. The authors should characterize the uncertainties/statistical errors on the measured free energy profiles to better evaluate the significance of change (e.g. for inspiration: https://www.plumed.org/doc-v2.7/user-doc/html/masterclass-21-2.html).

In response to the reviewers' comment, we have included a new sub-section in materials and methods together with an additional figure in the Supplementary Information (Figure S13), as follows:

"Error: We estimated the error on the 2D free energy landscape of the first collective variable (CV1), which is the TM3-TM6 intracellular ends distance (Figure S13) using the block averaging technique, as described in the PLUMED tutorial on calculating error bars (https://www.plumed.org/doc-v2.8/user-doc/html/lugano-4.html). We calculated the weights using the metadynamics bias potential obtained at the end of the simulation, and assuming a constant bias during the entire course of the simulation.[28] Specifically, we calculate the error using blocks of histograms of 25 ns each, covering the entire 250 ns simulation time."

c. In the cMD trajectories, a large part of phase space is sampled, which does not appear consistent with what one would expect based on the free energy landscapes. For instance, it does not seem reasonable to cover an almost complete conformational transition in 500ns when the barrier of the system is on the order of 5-8kcal/mol. The definition of CVs may have led to an overestimation of the free energy barrier. Hence an independent validation of the free energy barrier height is needed, by e.g. changing the CV definition.

We agree with the reviewers' that the cMD simulations cover a large part of the phase space. This is in part due to running simulations staring from both the inactive and active structures. For the latest, we removed the G-proteins from the receptor. This situation increases the flexibility of the receptor and induces a population shift respect to the starting point. However, as expected, we did not observe any complete transitions in our cMD simulations either staring from the inactive or active structures (see Figure 1C and S2).

Regarding the activation energy barrier, we would like to clarify that the aim of our study is not to compare subtle differences in energy barriers after system perturbations or compare them with experimental data. As far as we know, there is not NMR data available that confirms the exact time-scale of activation for A1R receptor, suggesting that A1R could be highly flexible. Notably, we report a rather low activation energy barrier of approximately 4 kcal/mol derived from the metadynamics simulations of A1R in the presence of adenosine. This is consistent with other computational studies of A1R where a complete transition from active to inactive [PNAS 2022, 119, E2203702119] and from inactive to pre-active [Nature 2021 597, 571] states is sampled in the course of nanosecond-scale Gaussian accelerated MD simulations. In addition, similar activation barrier values have been computed for the b2 adrenergic GPCR in the presence of adrenaline using different collective variables, as reported in [PLoS Comput. Biol. 2011, 7, e1002193] and [eLife 2021, 10, e60715]."

After careful consideration, we found relevant to validate our path of conformations by reweighing of our free energy into other collective variables. As previously stated, we have reweighted the original free energy into the ionic-lock, PIF motif, water-lock and toggle micro-switches (refer to the last paragraph of Essential revision 2.1 and Figure S5 and S6). Our analysis reveals that our original CV2 (TM6 torsion), the PIF motif, and the toggle display modest energy barriers, while our original CV1 (TM3-TM6 distance) presents a rather high energy barrier. Moreover, the ionic-lock and the water-lock exhibit the highest energy barriers. Thus, if we had chosen to use our initial CV1 and the PIF motif, we would have obtained a similar energy barrier, whereas choosing our initial CV1 and the water-lock would have resulted in a higher energy barrier, as predicted by our reweighting calculations (see Figure S7).

As mentioned in the manuscript, this data highlights the ability of our simulations to reproduce the activation pathway and provides interesting insights that can guide the selection of collective variables for future GPCR landscape calculations.

1. Configurations extracted from both conventional MD and wt-metadynamics are mixed in the analyses of the allosteric networks and the pockets. A more accurate way to integrate these datasets would be to modulate the weights of the configurations by their statistical weights, which can be retrieved from the metadynamics simulations.

We thank the reviewers for this suggestion and we will consider to use configurations by their statistical weights in future work. For this case, we aimed to include as much as configurations as possible from each conformational state. We then included all configurations from the inactive, intermediate and pre-active derived from the metadynamics and for the fully-active we applied a stride value in order to collect a similar number of structures.

1. Related to Figure S6, it is essential to compare the dynamics for all of the key class A activation motifs including the Na binding site, PIF motif, and NPxxY.

Based on the reviewers' comments, we have generated histograms for the relevant micro-switches corresponding to the inactive, intermediate, and pre-active states (see Figure S10). This analysis provides further support to the activation pathway derived from the metadynamics simulations. Notably, the population distributions of these micro-switches in the inactive, intermediate, and pre-active states exhibit a correlated progression that mirrors the receptor's activation pathway.

1. Please provide clarification on why 500 ns was chosen as the time-scale of the MD simulations and inclusion of the time course for the three independent MD simulations for each of the key structural features (e.g. TM6 torsion angles and TM3-TM6 distances).

To ensure adequate initial sampling of receptor activation, we performed three independent MD replicas of 500 ns each, starting from both the inactive and active structures. The purpose of these MD simulations is to provide an initial sampling of the receptor instead of describing the complete activation pathway. Based on this initial sampling, we selected a path of 10 conformations as starting points for the walker metadynamics simulations. We have added this information to the text for clarification.

"For each starting point we computed 3 replicas of 500ns, which is a reasonable simulation time to provide an initial sampling of the receptor activation."

1. The validation of the results in the form of previously published mutagenesis results does not appear completely convincing. Large parts of the protein are included in the allosteric network, making it likely that mutations in some of these residues will have an effect if mutated. In addition, the fact that mutations in ECL2 and ECL3 affect allostery is expected and does not constitute a good validation of the results. If no other results are included, we recommend that the language be toned down so as not to overstate the significance of the results.

Following the reviewers' comment, we have removed the following sentences from the results:"Among the PEN residues, we successfully captured most of the allosteric residues previously identified by mutagenesis studies, which highlights the reliability of the allosteric networks computed" and "The high predictive power of the PEN to identify allosteric residues highlights the reliability of the characterized allosteric pathways"

1. What is the justification for using an energy-based scoring for network analysis, given that a conventionally correlation-based approach has been used successfully in the field? The concern with an energy-based approach is that the interaction energy calculations do not consider the dielectric effect, i.e., if water molecules interfere with two interacting residues. Since the dynamic network is one of the critical aspects of this study, we believe the authors need to explore other tools such as the one implemented in VMD (https://www.ks.uiuc.edu/Research/vmd/plugins/networkview/) and compare the results.

We decided to perform protein energy networks analysis because our aim was to investigate how the networks change in different conformational states along activation. We selected this approach because energy networks can provide a more detailed insight into how communication within the protein changes during activation, as compared to cross-correlation networks, which are more suited to characterizing communication through correlated motions in the global ensemble. In order to compare both protein energy networks and correlation networks we performed the cross-correlation analysis in the global ensemble. Note that both approaches yield some similarities and provides complementary information.

We also would like to thank the reviewers for raising concerns about the methodology employed in our work.We acknowledge that gRINN, which we used to generate the pairwise residue mean interaction energy matrix, does not include water molecules and ligands during the matrix generation process. As a result, we are unable to capture communication pathways that involve water-mediated connections or interactions between ligands and residues. For example, in the pre-active ensemble, Y2005.58 and Y2887.53 from the NPxxY motif are connected by a hydrogen bond facilitated by a bridging water molecule (the son-called water-lock). However, such communication is not captured in our analysis due to the absence of water molecules (Figure 3). We highlight this major limitation in the text. Another example can be observed in the simulation of the PAM-ADO-A1R-Gi2 system, where communication between L242 and S246, two residues involved in the Positive Allosteric Modulator (PAM) binding site, is missing in the PEN (Figure 8). Since these residues must be connected through the PAM, our methodology cannot detect their communication. A promising tool to considered in future studies is webPSN v2.0 [Nucleic Acids Res. 2020, 48, W95], a protein structure network analysis that includes nucleic acids and more than 30,000 biologically relevant molecules and ions, which is highly advantageous to study the effect of drugs on the protein communication.

1. Provide generic residue numbers such as GPCRdb or Ballesteros Weinstein numbering for all mentioned residues in text and figures, as is standard for structural papers.

As the reviewers suggested, we have renumbered all residues mentioned in the text and figures according to the Ballesteros Weinstein numbering scheme.

Additional suggestions for the authors to consider:

1. For the PEN analysis it would be useful to digest these communication networks with respect to the established structural activation motifs of class A GPCRs (Na binding site, PIF, and NPxxY) that are present at the A1R.

In order to make the PEN analysis more digestive, we have revised the second paragraph of the "Energy Networks captures the dynamic allosteric pathways along A1R activation" results section. Specifically, we have highlighted the most relevant micro-switches captured in the PEN, with a particular focus on the ionic and water-lock switches, which are the most prominent for the protein communication.

1. It is unclear why the authors chose two largely correlated CVs (See comment 2c). In addition, the choice of CV is likely contributing to the distortion of S6, as displayed in Figure 1E. It has been shown that choosing a different CV set that describes the motion between states in a more distributed way is more likely to lead to a converged conformational ensemble. We suggest repeating the metadynamics simulations with a more distributed CV set that encompasses all of the microswitches in the receptor.

Regarding the concern raised by the reviewers about the distortion observed in the TM6 end, we want to clarify that it is not attributed to the selection of collective variables (CVs) since it is already explored in the initial conventional MD simulations (see Figure S2B, W5 structure). We selected two CVs that may seem largely correlated, but they actually describe different aspects of the TM6 inward-to-outward transition. The first CV, which measures the distance between the center of mass of TM3 and TM6, is more related to the dynamics of the ionic lock in the intracellular region. On the other hand, the second CV (TM6 torsion) is related to the forces sensed by the upper region of TM6, including the dynamics of the W2476.48 toggle switch. Therefore, we believe that the combination of these two CVs provides a comprehensive description of the TM6 transition.

It is also worth mentioning that a more distributed set of CVs may be beneficial to better reproduce the activation energy barriers of the receptor. In fact, as shown in the reweighting calculations of the metadynamic bias potential (see Figures S6 and S7), using the TM3-TM6 COM end distances and the Y2005.58-Y2887.53 distance (water-lock) as CVs appears to be a good choice for this purpose.

1. To support the vision on how the analysis of activation pathway, energy networks and transient pockets could be used "to ease the design of allosteric modulators for A1R" (last sentence of the abstract), it might be necessary to show that the combination of these methods can indeed be predictive for the binding and effect of known ligands. This might provide a first step towards establishing that molecules that bind to pockets "near allosteric networks" is a promising avenue for drug discovery.

This highly relevant point has been addressed in Essential revisions 1.

1. The specific TM3-TM6 residues should be specified in figures and text. Commonly used TM3-TM6 comparisons include the measured maximum distance between 2x46 to 6x37, which could be used here also (e.g. see https://docs.gpcrdb.org/structures.html#structure-descriptors).

The specific residues of TM3 and TM6 that were used in the analysis have been clearly specified in both the Materials and Methods section and the figure captions of Figure 1 and 4.

1. Even though the "A1R in complex with PSB36 (PDB 5N2S)" is an inactive structure, PSB36 is an agonist. Hence, the authors should consider using the DU172 antagonist-bound structure for comparison (PPDB 5UEN)

According to literature, PSB36 is selective antagonist for A1R. In fact, experimental data showed that PSB36 exhibit low inverse agonist activity [Chem. Med. Chem. 2006, 1, 891]. Although PDB 5N2S and PPDB 5UEN structures are almost identical, the bulkier DU172 ligand causes a displacement of TM2 in the extracellular region. Therefore, we chose to use the 5N2S structure in our study. However, we will consider using the 5UEN structure in future studies.

1. How does adenosine and MIPS521 binding impact the different conformational states and PEN.

This highly relevant point has been addressed in Essential Revisions 1. For a more detailed analysis, refer to Figure 8 and S12, which shows the impact of MIPS521 on the PEN and the conformational landscape, respectively.

1. It would be interesting to note how the findings from this study compare/contrast to a very recently published report by Li et al, PNAS, 2022 "The full activation mechanism of the adenosine A1 receptor revealed by GaMD and Su-GaMD simulations". Similarly with regards to the determination of allosteric binding pockets in this recent publication: "The pocketome of G-protein-coupled receptors reveals previously untargeted allosteric sites" (https://doi.org/10.1038/s41467-022-29609-6)

According to the reviewers' suggestion, we have compared our findings to those of a recently published study [PNAS 2022, 119, E2203702119], which explored the full activation mechanism of A1R using both su-GaMD and GaMD.

This published work serves to further confirm the combined activation mechanism that we observed for A1R in our study, which entails the formation of a pre-active state in the presence of Adenosine and the stabilization of a fully-active state in the presence of both Adenosine and G-proteins. Moreover, their study reports the pre-activation of the receptor from the inactive state within 150 ns of GaMD, indicating a rather low activation energy barrier of the receptor in presence of Adenosine. This is consistent with the approximately 4 kcal/mol activation energy barrier we calculated for A1R-ADO in our 250 ns metadynamic simulations.

We would also like to highlight an additional noteworthy point we have included in the results as: "Notably, a recently published study reported that the orthosteric pocket contracts after ADO binding, as demonstrated by shortened distances of the so-called vestibular lid (defined as the sum of length of the triangle perimeters formed by E17045.51-Y2717.36-E17245.53 interacting residues) and the E17245.53-K26567 salt bridge.[48] Remarkably, the TM7-ECL3-ECL2 enhanced pathway by PAM effect contains the vestibular lid and the E17245.53-K26567 salt bridge residues (Figure 8). This suggest that PAM promotes the contraction of PB, leading to the stabilization of the ADO-bound state. Thus, the enhanced energy coupling between PB and PD may be responsible for the increase in the binding affinity of ADO in presence of the PAM, as observed experimentally.[19]"

1. A major advantage of allosteric drugs is the potential to achieve higher selectivity. Expansion of this study to include other adenosine receptor subtypes or linking to other types of molecular pharmacology (e.g. biased signalling, subtype selectivity, etc.) would be a major benefit to the field.

We are grateful to the reviewers for recognizing the potential impact of our work in various applications beyond our initial scope. We will consider to incorporate their valuable suggestions in our future research endeavors.

1. Consider including an explanation of the physiological and pharmacological relevance of A1AR in the introduction.

According to this suggestion, we have incorporated a new sentence in the introduction section as follows:

"The adenosine A1 receptor (A1R) is a member of the class A G protein-coupled receptor (GPCR) family that preferentially couples with Gi/o proteins. It is widely distributed in multiple organs mediating a variety of physiological processes, including those in the brain and the heart. Thus, A1R has significant therapeutic potential in the treatment of numerous diseases and disorders.[18]"

1. Even if not entirely necessary for the results, it would be more consistent if the study would include metadynamics of the G-protein bound state.

Performing a metadynamics calculation of the G-protein bound state is challenging as it requires careful consideration of the G-protein binding process. As a reference work, Giulio Mattedi et al. successfully implemented this calculation for the glucagon receptor [Proc. Natl. Acad. Sci USA, 2020, 117, 15414]. However, in our study the effect of the G-proteins in the activation landscape is a minor remark. Our study places a greater emphasis on sampling the most stable conformations associated with the fully-active conformational state to compute the protein energy networks.

1. Methods: "In other words, once the free energy surface does not change significantly during a relatively long period of time in the last part of the simulation". What is "relatively long period of time" and "change significantly". The convergence, should be stated as a quantitative description of the observed energy differences.

We have addressed this technical issue in Essential revisions 2. It is worth noting that "the relatively long period of time" required for convergence may vary depending on the specific system under study. Nonetheless, we believe that observing a stable energy surface over the course of 50-100 ns, while the system explores different relevant regions of the CV space, provides a good criterion for convergence."

1. The authors should strongly consider making their analysis code and simulation data publicly available (e.g. on GitHub or Zenodo) so that others can replicate and build upon this work.

We thank the reviewers for this suggestion. We will make all the output files generated from the get Residue Interaction eNergies and Networks (gRINN) calculation available to the public.By doing so, users will be able to visualize the results in the gRINN visual interface and perform customized network analysis using the pairwise residue mean interaction energy matrices. Additionally, we will provide all Pymol sessions that include the protein energy networks as well as the Isosurface representation of the frequency maps of the transient pockets. We believe that these materials will provide better visualization compared to the current figures presented in the manuscript and supporting information, which will be helpful in guiding future structure-based drug design campaigns.

(This is a response to peer review conducted by Biophysics Colab on version 3 of this preprint.)

Consolidated peer review report (28 November 2022)

GENERAL ASSESSMENT

The objectives of the study:

This paper aims to characterize the dynamics that drive allostery of the adenosine A1 receptor (A1R) via computational analysis of its activation free energy landscape and measurements of the appropriate geometrical parameters. This is done by focusing on the allosteric signaling pathways in different activation states, from inactive to active states via intermediate and pre-active ones, as well as the characterization of putative drug-binding pockets. The long-term objectives are to eventually be able to aid drug discovery efforts for this therapeutically important GPCR.

Key findings and major conclusions:

Conventional MD does not enable the sampling of the complete conformational landscape of receptor activation. Instead, enhanced sampling MD simulations are required to achieve this. Using metadynamics, the authors decipher the activation pathway of A1R, decode the allosteric networks and identify transient pockets. The protein energy networks computed throughout the inactive, intermediate active, pre-active and active conformational states unravel the extra and intracellular allosteric centers and the communication pathways that couple them, whereby the pathways are reinforced in the activated state. These conformations primarily differ in the dynamics of the ionic lock motif that couples TM3 to TM6 in the inactive conformation and reveal that G-proteins are required to fully stabilize the active conformation. Support for these findings comes from prior mutagenesis work on the A1R that identified key allosteric residues that in many cases map to identified communication nodes. Finally, the authors identified allosteric pockets throughout the A1R in four different conformational states that support prior experimental and MD studies on the mechanism of the positive allosteric modulator MIPS521 and which could be targeted for the design of modulators. Overall, these findings provide complementary support to a structure-based mechanism of activation and allosteric modulation of A1R, and extend the findings to incorporate dynamics across the full activation pathway.

The perceived strengths and weaknesses:

This preprint employs a combination of computational techniques to successfully reconstruct and analyze the conformational ensemble of the A1R activation. The metadynamics simulations supported the aim of the study, the results are clearly presented and the work is very well written. The authors could improve the discussion of how the protein energy network analysis could further advance rational design of specific modulators with a desired mode of action. The computational approach needs to be refined to be robust, with a focus on characterizing the convergence of the free energy landscapes. Overall, A1R is a good choice as the target for this study as there is existing structural and pharmacological data to support preliminary findings. Moreover, the framework presented herein could be adapted and scaled to other GPCRs with structural templates, which might enable comparison of allosteric pathways across families and classes.

RECOMMENDATIONS

Revisions essential for endorsement:

1.    The paper could better demonstrate how the insights gained herein will or could lead to progress in the rational design of specific modulators with a desired effect. The authors should outline and discuss how they envision the modeling pipeline they have designed will be used towards this goal and tone-down or explain why “this information is essential to ease the design of allosteric modulators for A1R.”. A recent study on FFAR1, where the authors targeted a specific dynamic pocket could be helpful in this respect (https://www.pnas.org/doi/full/10.1073/pnas.1811066116). Specifically this might entail: How does specificity for a receptor correlate with pockets forming in a specific state? From this, how does one design an agonist vs. an antagonist vs. an inverse agonist? Does breaking a specific network select a function of the drug? How would another group follow up on this work, for example in a virtual screening campaign?

2.    Free energy calculations:

a.    A proof of convergence of the free energy calculations is missing. The authors argue that obtaining landscapes that do not change over time is proof of convergence, but this is incorrect in well-tempered metadynamics. The fact that the heights of the Gaussians decrease over time guarantees that the landscape will be stable over time, and the way to check convergence is to show that the collective variables become diffusive after convergence. In addition, to validate that the choice of collective variables (CV) is actually appropriate, they should check that CVs that were not biased are also diffusive. This would be best studied by looking at the behavior of microswitches that were not considered, such as ones describing the PIF motif, the NPxxY motif, the ligand binding pose, etc.

b.    The authors should characterize the uncertainties/statistical errors on the measured free energy profiles to better evaluate the significance of change (e.g. for inspiration: https://www.plumed.org/doc-v2.7/user-doc/html/masterclass-21-2.html).

c.    In the cMD trajectories, a large part of phase space is sampled, which does not appear consistent with what one would expect based on the free energy landscapes. For instance, it does not seem reasonable to cover an almost complete conformational transition in 500ns when the barrier of the system is on the order of 5-8kcal/mol. The definition of CVs may have led to an overestimation of the free energy barrier. Hence an independent validation of the free energy barrier height is needed, by e.g. changing the CV definition.

3.    Configurations extracted from both conventional MD and wt-metadynamics are mixed in the analyses of the allosteric networks and the pockets. A more accurate way to integrate these datasets would be to modulate the weights of the configurations by their statistical weights, which can be retrieved from the metadynamics simulations.

4.    Related to Figure S6, it is essential to compare the dynamics for all of the key class A activation motifs including the Na binding site, PIF motif, and NPxxY.

5.    Please provide clarification on why 500 ns was chosen as the time-scale of the MD simulations and inclusion of the time course for the three independent MD simulations for each of the key structural features (e.g. TM6 torsion angles and TM3-TM6 distances).

6.    The validation of the results in the form of previously published mutagenesis results does not appear completely convincing. Large parts of the protein are included in the allosteric network, making it likely that mutations in some of these residues will have an effect if mutated. In addition, the fact that mutations in ECL2 and ECL3 affect allostery is expected and does not constitute a good validation of the results. If no other results are included, we recommend that the language be toned down so as not to overstate the significance of the results.

7.    What is the justification for using an energy-based scoring for network analysis, given that a conventionally correlation-based approach has been used successfully in the field? The concern with an energy-based approach is that the interaction energy calculations do not consider the dielectric effect, i.e., if water molecules interfere with two interacting residues. Since the dynamic network is one of the critical aspects of this study, we believe the authors need to explore other tools such as the one implemented in VMD (https://www.ks.uiuc.edu/Research/vmd/plugins/networkview/) and compare the results.

8.    Provide generic residue numbers such as GPCRdb or Ballesteros Weinstein numbering for all mentioned residues in text and figures, as is standard for structural papers.

Additional suggestions for the authors to consider:

1. For the PEN analysis it would be useful to digest these communication networks with respect to the established structural activation motifs of class A GPCRs (Na binding site, PIF, and NPxxY) that are present at the A1R.

2. It is unclear why the authors chose two largely correlated CVs (See comment 2c). In addition, the choice of CV is likely contributing to the distortion of S6, as displayed in Figure 1E. It has been shown that choosing a different CV set that describes the motion between states in a more distributed way is more likely to lead to a converged conformational ensemble. We suggest repeating the metadynamics simulations with a more distributed CV set that encompasses all of the microswitches in the receptor.

3. To support the vision on how the analysis of activation pathway, energy networks and transient pockets could be used “to ease the design of allosteric modulators for A1R” (last sentence of the abstract), it might be necessary to show that the combination of these methods can indeed be predictive for the binding and effect of known ligands. This might provide a first step towards establishing that molecules that bind to pockets “near allosteric networks” is a promising avenue for drug discovery.

4. The specific TM3-TM6 residues should be specified in figures and text. Commonly used TM3-TM6 comparisons include the measured maximum distance between 2x46 to 6x37, which could be used here also (e.g. see https://docs.gpcrdb.org/structures.html#structure-descriptors).

5. Even though the "A1R in complex with PSB36 (PDB 5N2S)" is an inactive structure, PSB36 is an agonist. Hence, the authors should consider using the DU172 antagonist-bound structure for comparison (PPDB 5UEN)

6. How does adenosine and MIPS521 binding impact the different conformational states and PEN.

7. It would be interesting to note how the findings from this study compare/contrast to a very recently published report by Li et al, PNAS, 2022 “The full activation mechanism of the adenosine A1 receptor revealed by GaMD and Su-GaMD simulations”. Similarly with regards to the determination of allosteric binding pockets in this recent publication: “The pocketome of G-protein-coupled receptors reveals previously untargeted allosteric sites” (https://doi.org/10.1038/s41467-022-29609-6)

8. A major advantage of allosteric drugs is the potential to achieve higher selectivity. Expansion of this study to include other adenosine receptor subtypes or linking to other types of molecular pharmacology (e.g. biased signalling, subtype selectivity, etc.) would be a major benefit to the field.

9. Consider including an explanation of the physiological and pharmacological relevance of A1AR in the introduction.

10. Even if not entirely necessary for the results, it would be more consistent if the study would include metadynamics of the G-protein bound state.

11. Methods: "In other words, once the free energy surface does not change significantly during a relatively long period of time in the last part of the simulation". What is “relatively long period of time” and “change significantly”. The convergence, should be stated as a quantitative description of the observed energy differences.

12. The authors should strongly consider making their analysis code and simulation data publicly available (e.g. on GitHub or Zenodo) so that others can replicate and build upon this work

REVIEWING TEAM

Reviewed by:

Antonios Kolocouris, Professor, Department of Medicinal Chemistry Faculty of Pharmacy National and Kapodistrian University of Athens, Greece:

CADD and computational biophysics on adenosine receptors

David Thal, Senior Research Officer, Monash University, Australia:

structural biology and molecular pharmacology of allosteric mechanisms underlying Class A GPCRs

SciLifeLab Journal Club, Stockholm, Sweden (see Appendix for members)

Curated by:

Alexander S. Hauser, Associate Professor, University of Copenhagen, Denmark

APPENDIX

SciLifeLab Journal Club:

Feedback was generated in a meeting of the journal club involving:

Lucie Delemotte (Journal Club oversight), Associate Professor of Biophysics, KTH Royal Institute of Technology, Sweden: modeling and enhanced sampling of GPCRs and other membrane proteins.

Olivia Andén, PhD student, Stockholm University: cryo-EM and functional characterization of membrane proteins.

Cathrine Bergh, PhD student, KTH Royal Institute of Technology: enhanced sampling simulations of membrane proteins.

Koushik Choudhury, PhD student, KTH Royal Institute of Technology: membrane protein modeling, enhanced sampling simulations.

John Cowgill, postdoctoral scholar, Stockholm University: cryo-EM and simulations of membrane proteins.

Chen Fan, postdoctoral scholar, Stockholm University: cryo-EM and simulations of membrane proteins.

Nandan Haloi, postdoctoral scholar, KTH Royal Institute of Technology: membrane protein modeling, free energy calculations, structure refinement in cryo-EM maps.

Rebecca J Howard, researcher, Stockholm University: membrane protein structure-function, allosteric modulation.

Marie Lycksell, PhD student, Stockholm University: structure and simulations of membrane proteins.

Antoni Marciniak, PhD student, KTH Royal Institute of Technology: enhanced sampling simulations of GPCRs and other membrane proteins.

Darko Mitrovic, PhD student, KTH Royal Institute of Technology: membrane protein modeling, enhanced sampling, machine learning.

Alex Payne, PhD student, Memorial Sloan Kettering Center for Cancer Research: membrane protein modeling, cryo-EM structure determination, drug discovery.

Urška Rovšnik, PhD student, Stockholm University: cryo-EM and functional characterization of membrane proteins.

Akshay Sridhar, postdoctoral scholar, KTH Royal Institute of Technology: membrane protein modeling, enhanced sampling simulations.

Amanda Dyrholm Stange, PhD student, Aarhus University: membrane protein modeling, enhanced sampling simulations.

(This consolidated report is a result of peer review conducted by Biophysics Colab on version 3 of this preprint. Minor corrections and presentational issues have been omitted for brevity.)

Consolidated peer review report (19 October 2022)

GENERAL ASSESSMENT

Pannexin hemichannels are a family of important large pore channels involved in ATP release during apoptosis and many other interesting biological processes. In this preprint, the authors present the first structure of pannexin-3 (PANX3) using cryo-EM, which has a similar overall fold to earlier structures of pannexin-1 (PANX1) but with several unique and interesting features within the pore, including regions where the dimensions and electrostatic potentials are quite unique and a more open lateral portal that may also serve as a permeation pathway. The authors also solve the structures of several mutants of pannexin1, including the disease-causing R217H mutation and several mutations of interesting pore-lining residues. The structures are complemented by electrophysiological measurements of ion conduction as well as ATP binding to explore alterations in ion conduction and how permeant anionic molecules like ATP may interact with the pore. The structure of PANX3 is a very important contribution to the field that will be of interest to many scientists, including those working on pannexin channels and other large pore channels. Although functional data are provided to help guide several key interpretations, they are difficult to evaluate as currently presented, and do not directly address key functional differences that may exist between PANX1 and PANX3, such as single channel conductance or ion selectivity.

RECOMMENDATIONS

Revisions essential for endorsement:

1) A systematic concern of the functional data is that it is not possible from the data presented to know how much of the current measured corresponds to leak or endogenous currents without showing data for untransfected cells obtained at the same time as PANX channel recordings. This is important to control for variability in the quality of recordings and expression of endogenous channels over different passages of the HEK cells. If representative, the currents from mock transfected cells in Supplementary Fig. 1 are reassuring, but it is important that such measurements are provided in all figures. It would also be important to spell out what mock transfection means. Were these untransfected cells or cells treated with transfection reagents + empty plasmids? This is a particular concern given that the one inhibitor, CBX, may have lower affinity for PANX3 than PANX1 and therefore cannot be used to identify the currents specifically related to PANX expression. It would be much more convincing if the authors could show I-V data throughout for both untransfected and transfected cells, before and after application of CBX, so that readers can get a sense of the current associated with PANX channels and differences in CBX sensitivity. It would also be good to show data at different CBX concentrations if the authors wish to draw conclusions about differences in CBX sensitivity. Michalski et al., 2018 provide one example of how to present functional data for PANX channels that gives the reader the necessary information to understand key findings. The authors should show a dotted line at zero current level when presenting currents like those shown in Supplementary Fig S1. It would also be best to present representative currents along with I-V and G-V data in the main figures. Finally, from the data presented in Supplementary Fig S1 it appears that the quality of voltage-clamp is at times suboptimal as a slow component is evident in the capacitive transients. Do the authors have sufficient data to select a subset of recordings where capacitive transients are single exponential and rapid, indicative of good voltage clamp speed, and to exclusively use those for presenting example recordings and constructing both I-V and G-V relations?

2) The data for PANX3 channel activity needs to be re-evaluated in light of contrasting data in the literature. Bruzzone et al., 2003 reported that PANX3-expressing frog oocytes do not respond to voltage steps and Michalski et al. 2018 reported that PANX3 is not functional when stimulated with depolarizing membrane voltage steps, even when surface expression was confirmed using surface biotinylation. This is an important point that the authors should try to address as they are the first to provide functional recordings of PANX3. This finding would be more conclusive if the authors could provide data for untransfected cells obtained side-by-side with that for PANX3-expressing cells. Again, providing data to compare key functional properties, such as ion selectivity, would be a valuable contribution to the field.

3) The lower current density observed for PANX1 R217H needs to be presented as outlined in point 1, but even then, this finding does not necessarily reflect a change in channel conductance as concluded. It could also be due to changes in surface expression, even though the overall protein expression is comparable to wt, as noted. It would be good to control for possible changes in surface expression, better document similar CBX sensitivity, and ideally measure the single channel conductance using single channel recordings. The shift of G-V observed for R217H in Fig 3e is interesting but the change in voltage-sensitivity is not convincing because the mutant G-V does not appear to be approaching saturation like wt. If G-V relations were obtained by simply dividing current by the difference between the test voltage and Vrev, as indicated, it would also be interesting to look at G-V relations by specifically using the CBX-sensitive current component to calculate G. Although CBX sensitivity may indeed vary for different constructs, the CBX-sensitive current is the most likely component to be associated with the PANX channel, and it would be interesting to see how it compares with the overall G-V.

4) The ATP binding data suggesting a decreased affinity for R217H is interesting, as is the decrease observed for the R128A mutant. The authors describe the 3-fold decrease in affinity for R24A as minimal, when it is similar to the difference noted earlier between PANX1 and PANX3, which is stated to be weaker. Importantly, no functional data are provided to assess whether R24A or R128 are functional, which is critical for understanding changes in ATP affinity. The text on the bottom of page 8 is also confusing because the authors state “We also observe reduced ATP binding, decreased current density and voltage-sensitivity in the mutant channel (Extended Data Fig 5b,c,e)” when it’s not clear what mutant is being referred to. Presumably R217H, but this needs to be clear, and data for R24A and R128A are needed.

5) The resolution of the present structures (3.75 to 4.29 Å) is quite modest; sufficient to determine the backbone fold but unlikely to contain adequate density for many side chains. The written presentation could be more nuanced and refer to the quality of side chain density in regions where differences between structures are discussed.

6) In the discussion, the authors propose that PANX3 is open, but by HOLE standards, this would apply to all solved structures of PANX channels. In addition, this conclusion overlooks the fact that the channel has minimal activity at 0 mV, as well as previous proposals about unresolved intracellular regions potentially occluding the pore and preventing permeation. Admittedly the C-terminus where caspase cleavage activates the channel is shorter in PANX3 compared to PANX1, but we still encourage the authors to be more circumspect when speculating about the functional state that their structures represent.

7) Interpretation of the PANX1 double mutant structure is difficult because PANX2 is only distantly related to PANX1, so it is unlikely that simply swapping two residues could elucidate the structural relationships, including how differences in a specific region of the pore may influence ion permeation or ion selectivity. Perhaps the author could provide a more compelling rationale by acknowledging the limitations and then put forward the mutant as an initial attempt to perturb an interesting region of PANX1 that is different to PANX3. If not, the authors might consider removing this data from the manuscript because it adds little to the study.

8) More information is required to interpret the ATP-binding assays. What is the relationship between the apparent ATP-dissociation constant and its permeability? Since those assays potentially also include non-specific interactions, additional support for the observed changes in ATP binding affinity could be provided by a negative control measuring binding to a membrane protein which is known not to interact with ATP. Also, the authors might consider using this assay to measure CBX binding for PANX1 and PANX3. A correlation with lower CBX sensitivity for currents would help to support that interpretation.

9) The preprint contains a number of statements that are speculative because they are not supported by data, which the authors should either remove or tone down. Examples include:

"Also, the movements of the aromatic group of F58 through its torsion angle can further alter the diameter of this constriction point and facilitate selective access to the pore".

"PANX isoforms do not display heterogenous oligomeric associations"

"A comparison with the Alphafold2 model of PANX3 with the experimental model in this study indicates that the N-terminus faces the cytosol. It constricts the channel from the cytoplasmic side, unlike PANX1WT, where the N-terminus lines the pore and interacts partially with the adjacent protomer"

"S70 and Q76 between two protomers form a hydrogen bond resulting in inter protomeric interactions leading to a stable heptamer"

"Extracellular loops and EH1 have an average shift of 1.5-2 Å away from the pore, which along with the slight TM1 movement, is most likely responsible for inducing the change in the W74 position by moving the tryptophan indole ring towards the pore, thereby shortening the pore radius by 4 Å"

“In comparison to the PANX1WT, the W74 shifts by a χ2 torsion angle of nearly 88.3° towards the pore leading to substantial closure of the pore diameter in PANX1 channels and affecting channel properties"

"The negatively charged surface in PANX3 may facilitate its role as an ER calcium channel"

Additional suggestions for the authors to consider:

1) 2) Given the unique electrostatic properties observed in the structure of PANX3 compared to PANX1, it would be interesting to undertake experiments looking at the relative permeabilities of the two channels to different anions and cations. Figure 3 in Michalski et al., 2020 contains measurements that could be useful to compare PANX1, PANX3 and some of the mutants studied here.

2) In Figure 3.d. and 4.c. the authors describe the channel physiology of PANX1 mutants and compare them with wt. Adding data for wt PANX1 would make it easier for the reader to understand what the authors wish to convey. Further, in Figure 2g, 3d, and 4c, the authors used normalized electrophysiological data to represent channel physiology, which is justified due to the minimal current through such large pore channels. However, because the methods section did not include the point of normalization for those measurements, including this information would provide a better basis for evaluation of those data points. Further as the authors mention in section “PANX3 displays a double-sieve pore organization”, the pore of PANX3 is lined with residues I74 and R75. While residue I74 is easily recognizable, R75 is not depicted. It would be interesting to see the orientation of these residues towards each other to get a better understanding of their placement and how they interact without consulting the deposited map. In addition, in the section “PANX3 displays a double-sieve pore organization”, the authors nicely describe the observation of a separation between TM2 and CTH1. Since the authors suggest the passage of ions through the separated parts, those findings could be further supported by an electrostatics surface representation of this area.

3) As described in section “PANX3 displays a double-sieve pore organization”, the authors suggest that the additional constriction site observed in PANX3 leads to the separation of two vestibules with significantly different electrostatic properties. The division of the channel pore allows the regulation of both ATP and Ca2+ ion release, particularly as the first vestibule compartment is thought to be important for Ca2+ binding. Therefore, mutations of the surface of the primary vestibule and the second constriction site, followed with electrophysiological characterization of Ca2+ and ATP release by mutants, would allow the authors to further strengthen their hypothesis.

4) Fig 2 does not do a very good job of illustrating many of the unique features of the external pore of PANX3 that are discussed at the bottom of pg 5 or in the middle of pg6. We suggest the authors work to improve the presentation in the figure to illustrate the unique features they wish to communicate. It would also be good to show a figure somewhere illustrating the unknown densities discussed on pg 6. What is the experimental evidence that the uncharacterized densities are not noise?

5) Ref 17 should be Michalski et al., 2020

6) In Fig 5 it would help to use grey or another unique colour for the HOLE representations to more clearly distinguish the pore from the protein.

REVIEWING TEAM

Reviewed by:

Toshi Kawate, Associate Professor, Cornell University, USA: structure and mechanisms of pannexin channels

Elena Farah Lehmann, graduate student, University of Zurich, Switzerland: structural biology, cryo-EM, large pore channel families

Kenton J. Swartz, Senior Investigator, NINDS, NIH, USA: ion channel structure and mechanisms, chemical biology and biophysics, electrophysiology and fluorescence spectroscopy

Curated by:

Kenton J. Swartz, Senior Investigator, NINDS, NIH, USA

(This consolidated report is a result of peer review conducted by Biophysics Colab on version 1 of this preprint. Minor corrections and presentational issues have been omitted for brevity.)

Authors’ response (22 February 2023)

GENERAL ASSESSMENT

In this preprint, Flores-Aldama and colleagues set out to identify molecular determinants of fast inactivation in the TRPV6 ion channel, a mechanism not observed in the closely related TRPV5 channel. The work focuses on the helix-loop-helix (HLH) motif, which is a region of the channel at the interface between the intracellular and transmembrane domains, the S2-S3 linker and the TRP Domain helix (TDh). Through MD simulations, the authors identify pairs of amino acid residues in the HLH/S2-S3 linker/TDh structural triad that move differently in TRPV5 and TRPV6 based on available cryo-EM structures. They mutate the E288 residue in TRPV6 to D, which is its counterpart in TRPV5, and make the reverse mutation in TRPV5, and show that swapping this single residue is sufficient to transfer the inactivation kinetics between the two channels. They also show that the E294A mutation in the HLH partially reduces fast inactivation in TRPV6 and that the K245A mutation in ARD6 in TRPV5 confers some fast inactivation to that channel, albeit less than that observed in TRPV6. A very rewarding aspect of the manuscript is that some of the structural hypotheses were arrived at through an evolutionary analysis of sequences from many orthologues of both channels. This work is a follow up to the authors’ previous publication (https://doi.org/10.1038/s41598-020-65679-6), where they identified the HLH as a region important for fast inactivation in TRPV6. The manuscript includes new data that provides insight into the different inactivation mechanisms in these channels and strengthens the notion that the HLH linker region plays an important role in channel gating.

RECOMMENDATIONS

Revisions essential for endorsement:

1. Structural comparisons are made between TRPV5 and TRPV6 structures that were determined in different labs, under different conditions, expression systems, etc., so whether the differences are due to Ca2+ or other experimental conditions is unclear. Also, the inactivated structures are all obtained in the presence of calmodulin, so whether the changes are due to calcium or calmodulin is also unclear. Finally, some of the noninactivated structures are partially open, while some are closed. The authors should clearly state these caveats and fully discuss the limitations of the inferences obtained from this analysis.

The critique is reasonable, and we were well aware of the diversity of structures we were dealing with. The only way we devised to partially surmount the caveat was to group them and study the average distances. By doing this, we observed that the two groups (i.e. presumably inactivated/versus presumable non-inactivated) consistently showed similar distances between the critical amino acids described in the text. We performed additional molecular dynamics simulations for the mutant channels and overall the trend in the change in distances was conserved. We edited the text accordingly and tone down the discussion regarding this point.

1. Molecular dynamics (MD) simulations were carried out in the presence of a non-physiological (50 mM) Ca2+ concentration, presumably to increase the chance of observing a conformational change. However, throughout the duration of the simulation, no Ca2+ binding events were observed, thus leading the authors to conclude that Ca2+ induced an inactivating conformational change through global effects. It is not clear to the reviewers what the authors intend to convey with this conclusion. The high calcium concentration will increase ionic strength by a very large amount, thus affecting any electrostatic interactions through charge screening. If this is the case, the same effects on inactivation should be expected from recordings (and simulations) in high ionic strength, thus weakening the finding that this is a specific effect of calcium. New experiments to probe these effects should be carried out, but if this is not possible, the authors should tone down their conclusion of a specific effect of calcium on inactivation.<br />

This is correct we used 50mM in the simulations hoping to accelerate the process. We actually observed calcium binding, however, not in the interphase described here but rather at the ankyrin repeats (also associated to the mechanism described here). The revised version contains this information describing the location of the binding sites. The binding was concentration dependent and we observed even at 10mM calcium. Following the critique, we calculated the effects induced by charge in the simulations and was not significant. Additional experiments were performed with barium in the external solution showing a high specificity for calcium.

1. The physiological importance of the fast inactivation in TRPV6 is unclear. While there is a clear, evolutionarily conserved difference between TRPV5 and TRPV6, these channels are unlikely to experience fast 50 ms voltage jumps where this fast inactivation difference would be observable. Rather they are expressed in epithelial cells with stable, or slowly changing membrane potential. At longer time scales, the two channels show similar levels of inactivation, because they both undergo slow inactivation mediated mostly by calmodulin, which is an abundant protein expressed in essentially every cell type. The authors should discuss whether they think fast inactivation is physiologically relevant in these channels or under what conditions they expect it to be relevant.

The physiological relevance of the fast inactivation in TRPV6 channels is somewhat important, but not critical, as, independently of our physiological understanding of the phenomena, it does exist, making it intrinsically interesting from a biophysical/evolutionary perspective. Nevertheless, we think TRPV6's fast inactivation might be relevant in intestinal epithelia, so we added a short note about it in the revised text:

In a previous study, we reported an expansion of the expression profile in mammalian TRPV6 compared to TRPV5. TRPV6, besides being expressed in the kidneys -where the [Ca2+]ext is regulated under physiological conditions-, is also expressed in the intestine (1). At this organ, TRPV6 is exposed to quick changes in the [Ca2+]ext after every meal. We reasoned that the fast inactivation phenotype of mammalian TRPV6 plays a critical role in protecting the intestinal epithelial cells from a Ca2+ overload and consequent apoptosis. In agreement with our rationale, TRPV6 expression is regulated by dietary Ca2+ levels (2-4) and its relevance in intestinal epithelial barrier dysfunction was recently discussed by Mori et al. (5).

1. Flores-Aldama L, Vandewege MW, Zavala K, Colenso CK, Gonzalez W, Brauchi SE, et al. Evolutionary analyses reveal independent origins of gene repertoires and structural motifs associated to fast inactivation in calcium-selective TRPV channels. Sci Rep. 2020;10(1):1–13.

2. Hoenderop JGJ, Dardenne O, Van Abel M, Van Der Kemp AWCM, Van Os CH, St -Arnaud R, et al. Modulation of renal Ca2+ transport protein genes by dietary Ca2+ and 1,25-dihydroxyvitamin D3 in 25-hydroxyvitamin D3-1alpha-hydroxylase knockout mice. FASEB J. 2002;16:1398–406.

3. Song Y, Kato S, Fleet JC. Vitamin D receptor (VDR) knockout mice reveal VDR-independent regulation of intestinal calcium absorption and ECaC2 and calbindin D9k mRNA. J Nutr. 2003;133(2):374–80.

4. Van Cromphaut SJ, Dewerchin M, Hoenderop JG, Stockmans I, Van Herck E, Kato S, et al. Duodenal calcium absorption in vitamin D receptor-knockout mice: functional and molecular aspects. Proc Natl Acad Sci U S A. 2001;98(23):13324–9.

5. Mori Y, Omori M, Nakao A. Vital but vulnerable: Human TRPV6 is a trade-off of powerful Ca2+ uptake and susceptibility to epithelial barrier dysfunction. Cell Calcium [Internet]. 2022;107(September):102652.

1. The charge reversal mutation experiments, though interesting, need to include the opposite mutation in the “interacting” partner in order to convincingly conclude that interacting pairs of charged residues are determinants of inactivation. In its current form, the manuscript does not provide conclusive evidence of interactions, rather, it only raises the possibility. The authors should tone down this conclusion.

The reviewers are correct. The result might not be definitive and just rises a possibility. By additional simulations and analysis, we tried to mitigate the point raised and following reviewer’s advice we toned down the discussion of the issue.

Additional suggestions for the authors to consider:

1. The study will be easier to comprehend if the authors expand the introduction to provide a better description of the structure of these two channels, and specifically, the regions interrogated in this study.<br />

Both the introduction and first section were edited accordingly.

1. The communication of the main findings in the study would be enhanced if the authors provide a better description of previous work on these channels and clearly state the gaps in our current knowledge that their study addresses.

We did the best effort to address this critique in the revised version.

1. TRPV1-4 are so different from TRPV5 and TRPV6 in many aspects that discussion about them in the context of fast inactivation is probably not relevant.

Although we tone down the text to address the critique, we kept the data in supplementary figures and the idea at the discussion section, just because we think it is relevant and because they are not as dissimilar as the reviewers want to think. From our perspective, the evolution of temperature dependent phenotypes and the evolution of calcium dependent inactivation in TRPV5/6 points to the same region where multiple signals are integrated. In fact, we envision that the molecular rearrangements that underly both phenotypes will end up being very similar.

1. For all figures, include the n for each experiment and increase the size of symbols for individual experiments in scatter plots.

We address the point together with providing averaged current densities (not only the normalized response) for the individual conditions.

Consolidated peer review report (15 December 2022)

GENERAL ASSESSMENT

In this preprint, Flores-Aldama and colleagues set out to identify molecular determinants of fast inactivation in the TRPV6 ion channel, a mechanism not observed in the closely related TRPV5 channel. The work focuses on the helix-loop-helix (HLH) motif, which is a region of the channel at the interface between the intracellular and transmembrane domains, the S2-S3 linker and the TRP Domain helix (TDh). Through MD simulations, the authors identify pairs of amino acid residues in the HLH/S2-S3 linker/TDh structural triad that move differently in TRPV5 and TRPV6 based on available cryo-EM structures. They mutate the E288 residue in TRPV6 to D, which is its counterpart in TRPV5, and make the reverse mutation in TRPV5, and show that swapping this single residue is sufficient to transfer the inactivation kinetics between the two channels. They also show that the E294A mutation in the HLH partially reduces fast inactivation in TRPV6 and that the K245A mutation in ARD6 in TRPV5 confers some fast inactivation to that channel, albeit less than that observed in TRPV6. A very rewarding aspect of the manuscript is that some of the structural hypotheses were arrived at through an evolutionary analysis of sequences from many orthologues of both channels. This work is a follow up to the authors’ previous publication (https://doi.org/10.1038/s41598-020-65679-6), where they identified the HLH as a region important for fast inactivation in TRPV6. The manuscript includes new data that provides insight into the different inactivation mechanisms in these channels and strengthens the notion that the HLH linker region plays an important role in channel gating.

RECOMMENDATIONS

Revisions essential for endorsement:

1. Structural comparisons are made between TRPV5 and TRPV6 structures that were determined in different labs, under different conditions, expression systems, etc., so whether the differences are due to Ca2+ or other experimental conditions is unclear. Also, the inactivated structures are all obtained in the presence of calmodulin, so whether the changes are due to calcium or calmodulin is also unclear. Finally, some of the non-inactivated structures are partially open, while some are closed. The authors should clearly state these caveats and fully discuss the limitations of the inferences obtained from this analysis.

2. Molecular dynamics (MD) simulations were carried out in the presence of a non-physiological (50 mM) Ca2+ concentration, presumably to increase the chance of observing a conformational change. However, throughout the duration of the simulation, no Ca2+ binding events were observed, thus leading the authors to conclude that Ca2+ induced an inactivating conformational change through global effects. It is not clear to the reviewers what the authors intend to convey with this conclusion. The high calcium concentration will increase ionic strength by a very large amount, thus affecting any electrostatic interactions through charge screening. If this is the case, the same effects on inactivation should be expected from recordings (and simulations) in high ionic strength, thus weakening the finding that this is a specific effect of calcium. New experiments to probe these effects should be carried out, but if this is not possible, the authors should tone down their conclusion of a specific effect of calcium on inactivation. 

3. The physiological importance of the fast inactivation in TRPV6 is unclear. While there is a clear, evolutionarily conserved difference between TRPV5 and TRPV6, these channels are unlikely to experience fast 50 ms voltage jumps where this fast inactivation difference would  be observable. Rather they are expressed in epithelial cells with stable, or slowly changing membrane potential. At longer time scales, the two channels show similar levels of inactivation, because they both undergo slow inactivation mediated mostly by calmodulin, which is an abundant protein expressed in essentially every cell type. The authors should discuss whether they think fast inactivation is physiologically relevant in these channels or under what conditions they expect it to be relevant.

4. The charge reversal mutation experiments, though interesting, need to include the opposite mutation in the “interacting” partner in order to convincingly conclude that interacting pairs of charged residues are determinants of inactivation. In its current form, the manuscript does not provide conclusive evidence of interactions, rather, it only raises the possibility. The authors should tone down this conclusion.

Additional suggestions for the authors to consider:

1. The study will be easier to comprehend if the authors expand the introduction to provide a better description of the structure of these two channels, and specifically, the regions interrogated in this study. 

2. The communication of the main findings in the study would be enhanced if the authors provide a better description of previous work on these channels and clearly state the gaps in our current knowledge that their study addresses.

3. TRPV1-4 are so different from TRPV5 and TRPV6 in many aspects that discussion about them in the context of fast inactivation is probably not relevant.

4. For all figures, include the n for each experiment and increase the size of symbols for individual experiments in scatter plots.

REVIEWING TEAM

Reviewed by:

Reviewer #1: TRP channel structure-function relationships and ion channel biophysics

Reviewer #2: TRP channel physiology and biophysics

León D Islas, Professor, National Autonomous University of Mexico, Mexico: ion channel biophysics, TRP channels

Curated by:

León D Islas, Professor, National Autonomous University of Mexico, Mexico

Authors' response (24 January 2023)

GENERAL ASSESSMENT

The rationale behind the study:

While the activation mechanisms of Class A and Class B GPCRs have been extensively studied. little emphasis has been placed on the study of the dynamics of class F receptors such as Smoothened (SMO). Hence it is still elusive which motifs may take part in the transition from inactive to active conformations. Understanding the underpinnings of receptor activation in terms of residue networks. and their modulation by allosteric modulators. could help rational drug design. such as for novel SMO antagonists for cancer treatment.

Key findings and major conclusions:

Bansal, Dutta and Shukla perform extensive molecular dynamics (MD) simulations in conjunction with Markov State Model theory for a range of conformational starting points (apo. agonist. and antagonist bound states) to elucidate a dynamic overview of SMO activation. This has mostly remained elusive despite the availability of inactive and active-state SMO structures. They reveal conserved motifs important for activation of class F receptors, which are distinct from other known activation motifs. including from class A or B GPCRs. The long-range MD simulations together with free energy calculations also identified three additional intermediate states between inactive and fully active SMO. Furthermore. they provide structural support for how the specific function of antagonists and agonists modulate the cholesterol tunnel and thereby modulate SMO's activity. Finally. the authors present the dynamic allosteric pathway at atomistic resolution between the extracellular and intracellular side during activation and upon ligand modulation. Taken together, the authors provide a more detailed understanding of Class F GPCRs that could serve as the foundation for specific experimental validation studies.

The perceived strengths and weaknesses:

The new perspectives on the conformational changes during activation of SMO are based on well-described MD simulations. The Class F activation mechanism is not well understood: hence the authors· conclusions advance the field by identifying states that are distinct from class A GPCRs and how cholesterol can modulate SMO's activity, resulting in a map of allosteric pathways for this receptor type. However, the stated uniqueness or proposed Class F-specific observations would be more definitive with additional analyses.

We sincerely thank the reviewers for providing insightful and constructive comments on our work. We believe that the reviewers' suggestions have improved the quality and clarity of the manuscript. The consolidated report was extremely helpful.

Based on the reviews, we extensively revised the main text and figures to accommodate the suggestions and required additional calculations.

RECOMMENDATIONS

Revisions essential for endorsement:

1. The title seems too comprehensive for the present study. Please consider a title that more accurately summarizes the specific work in this manuscript.

We thank the reviewer for this suggestion. However, unfortunately the manuscript is under review and the title has already been submitted to the journal.

1. [Methods - Pre-Production MD, page 20]: The authors chose a more complex membrane composition to mimic physiological cerebellar membranes that requires additional attention during equilibration. If this has not been undertaken (no note in the method section). we do recommend carefully investigating the lipid distributions/clustering. including unusual curvature, that might influence the receptors behaviour throughout the simulations, in particular if modulations by ligands are interpreted.

We thank the reviewer for this concern. The equilibration performed was performed for 40ns, and we found no unusual curvature changes on visual inspection. Regarding the lipid distribution, we have plotted the cholesterol distributions for the ensembles and observe a conformation-dependence on lipid organization in the membrane. We plotted the x-y distribution of cholesterol in both the leaflets in the membrane and do observe that cholesterol shows a concentrated density between TM2 and TM3 in inactive SMO. This concentration of cholesterol, however, is not seen in active SMO (both leaflets) and inactive SMO (lower leaflet). This further provides evidence that SMO indeed shows a propensity to cholesterol in the inactive state, given that cholesterol is the endogenous activating molecule for SMO. This additional discussion has been added to the manuscript for further clarification.

Added text: Results and Discussion, SMO's Activation is linked to opening of a hydrophobic tunnel.

"Interestingly, we observe a conformational dependence of the lipid organization in the membrane - Inactive SMO surrounds itself with a cholesterol in the upper leaflet, as opposed to other cases (Fig. S20). This suggests that cholesterol shows a propensity to accumulate outside inactive SMO to possibly transport itself in the hydrophobic tunnel, leading to SMO activation."

1. [Methods]: The authors should discuss convergence of the simulated clusters and energy landscape prior to conducting Markov State Modeling.

We thank the reviewer for this concern. The convergence of the energy landscape and the simulated clusters can be corroborated by the presence of continuous density between the inactive and the active states along time-independent component 1 in the tIC landscape (Fig. S9). The tIC plot shows the kinetically slowest processes, hence the simulated data has sampled the full conformational landscape associated with SMO activation. We have added additional text in the manuscript for further clarification.

Added text: Results and Discussion, SMO activation involves a conserved molecular switch.

"The convergence of the data, clusters and hence the free energies derived from it, were confirmed by the presence of a continuous density of data along tIC 1 (Fig. S9A). This shows that the simulations have indeed sampled the conformational landscape necessary to probe the activation pathway of SMO."

1. DRY motif:
2. Please clarify the statements about generalisation in Class F in light of the missing outward kinking. As this praline is present in other Class F receptors. it suggests that this activation feature is likely unique to SMO. Also this molecular switch should be compared to e.g. Rhodopsin. Which also signals through Gi (see e.g. Hofmann et al. doi:10.1016/j.tibs.2009 .07.005)

We thank the reviewers for this additional clarification. Text has been added to the manuscript to reflect the changes suggested.

Modified Text: Results, SMO activation involves a conserved molecular switch:

"This particular feature is hence unique to the activation mechanism of SMO."

• The authors should consider additional evidence or be more careful in their statement that the conserved motif (W3.50-G5.39-M6.30) acts as a microswitch in SMO signal transduction. The authors claimed that it is analogous to the DRY motif in class A GPCRs. However, the DRY motif has been shown to be involved in both inactive and active states. validated by experimental data. The R3.50 in DRY motif forms an ionic lock in the inactive state and this ionic interaction is broken during receptor activation. It is unclear what interactions are formed between the W-G-M motif in SMO.

We agree, and further experimental validation is required for establishing a role for the WGM motif. We posit that this motif works as a microswitch, mediated by hydrophobic interactions. The text in the manuscript has been modified to clarify this.

• Similar to W-G-M, the D-R-E motif has also been claimed as an important site for signal transduction. We recommend caution in this conclusion. The authors mentioned there is an H-bond interaction between D473 and E518. Is there a water molecule between these two residues? The two residues have very low pKa for the carboxylate group and probably are devoid of hydrogens in physiological conditions. Figure 2C should include the R400.

The pKa of the E518 has been evaluated using the H++ server, and E518 was found to be protonated under physiological conditions. Hence the presence of a H-bond between D473 and E518 is plausible. We have added additional clarification in the methods section to clarify this point. R400 has been included in the figure.

1. The statement "SAG acts as an agonist by allosterically expanding the tunnel at the cholesterol interaction site" (line 252) may be incorrect according to at least two lines of evidence: 1) elongation of the 4-aminomethyl group of SAG converts it to an antagonist; 2) SMO variants containing mutations at the cholesterol binding site don't respond to SAG as described in Deshpande et al (Nature 571. 284-288 (2019)). The agonist activity of SAG is most likely due to blocking cholesterol in the 7-T Ms. The authors may want to change the statement and conclusion or provide strong evidence to support it.

We agree, and the statement "SAG acts as an agonist by allosterically expanding the tunnel at the cholesterol interaction site" supports both the conclusions mentioned above. The following justification is provided:

• SAG's binding position lies right outside the proposed tunnel for cholesterol transport, making it a viable candidate as an agonist for SMO. The leading hypothesis for cholesterol transport-like endogenous activity for SMO states that the cholesterol enters the protein through the membrane, considering that previous structures (Byrne et al., Nature, 2016) have posited that a cholesterol must exit the plasma membrane in order to activate SMO. The antagonist-like activity of the addition of the 4-aminomethyl moiety may be alternatively explained as follows: The addition of the 4-aminomethyl moiety probably precludes the opening of the tunnel in the membrane by blocking the allosteric communication, and hence precludes cholesterol transport to the core TM from the membrane. However, further experimental validation is required for probing the exact role of the 4-aminomethyl moiety in SAG. Additionally, recent studies have provided further evidence for the CRD site being the orthosteric binding site for endogenous activation mechanism of SMO (Kinnebrew et al., eLife, 2021; Kinnebrew et al., Sci. Adv., 2022). For cholesterol to reach the orthosteric binding site, the tunnel must open between the membrane and the TM domain. We find through our studies that SAG-bound SMO shows such an opening, specifically between TM2 and TM3, which has been shown to be a binding site for cholesterol. (Hedger et al., Structure, 2019). Additionally, this opening is also present in the upper leaflet, which has been shown to be the leaflet through which PTCH controls SMO's activity. (Kinnebrew et al., eLife, 2021).

• Regarding the mutations in the cholesterol binding site which make it insensitive to SAG binding, these observations can also be explained based on the requirement of cholesterol to transport to the orthosteric binding site (the CRD site) for endogenous activation. Further extensive experimental evidence is hence required to completely understand the endogenous activation mechanism of SMO.

We sincerely thank the reviewer for this question.

Additional suggestions for the authors to consider:

1. [Fig S.19]: Validity of the MSM on 5 macrostates via the Chapman-Kolmogorov test: the predictions and estimates look identical. Please add a 95% confidence interval and provide scripts used for the calculation and plotting.

We thank the reviewer for this suggestion. Error has been estimated using bootstrapping for the 5-macrostate MSM. Bootstrapping was performed on 200 sets of randomly selected 80% trajectories. The errors have been added to the Chapman-Kolmogorov test and the scripts have been uploaded to the github link.

1. Did the authors try to simulate SMO with cholesterol bound to the cysteine rich domain (CRD)? The reorientation of CRD revealed by xSMO crystal structures is controversial in the field because this movement may be a result of crystal packing. It will be very interesting to test whether CRD can undergo this reorientation after cholesterol binding by MD simulation.

Unfortunately, the simulations of cholesterol bound SMO are outside the scope of this manuscript. We however do thank the reviewer for their suggestion.

1. [Methods, page 19 line 332]: It is not entirely clear what preparation was done to the SANTl-SMO structure. Please rephrase the sentences to ensure reproducibility.

We thank the reviewer for this suggestion. We have rephrased the preparation steps for SANT1-SMO structure for further clarity.

Edited text: Methods, MD Simulations, Simulation Setup

"For SANT1-SMO, owing to the lack of the CRD in the SANT1-SMO complex (PDB ID: 4N4W(35)), we sought to use the inactive orientation of 5L7D (inactive SMO, CRD present) instead. The SANT1-bound crystal structure (4N4W) was aligned to inac-SMO 5L7D (to maintain the same binding pose for SANT1), and the 5L7D-SANT1 starting point was used for simulations."

1. [Methods]: General structure preparation: Where the structures solvated prior insertion into the membrane to avoid collapsing of cavities?

The protein structures were prepared using the CHARMM-GUI webserver, which uses an optimized library of lipid conformations to prevent formation of cavities in the membrane. Hence the need to solvate the structures a priori was obviated.

1. [Methods - MD, page 20]: The authors do not mention the used force-field. Please add.

The force-field used for all simulations was CHARMM36. The force field has been mentioned in the Methods section.

1. [Figure S6]: For clarification and comparison (in context of uniqueness). Please show the changes in the residues involved in the microswitch for b2AR (6.30, 5.58. 5.66 - also shown for Rhodopsin and others).

The changes for the appropriate microswitch have already been shown in the figure.

1. [Figure 3]: the authors compared the CRD-TMD junction between inactive and active states. How is the conformation of these residues compared to the determined structures of SMO?

The conformation of the residues is the same as the determined structures of SMO. We have added an additional figure to compare the structure with the inactive-active structures of SMO.

1. [Results]: It is very interesting that three intermediate states have been determined between inactive and active states. It is unclear how these states (11., 12, 13) are defined, besides the energy barrier. Are there any signature residues or motifs that can represent each intermediate state?

The states I1-3 have been defined purely on the basis of free energy differences. Attempts to uniquely identify motifs present in each state I1-3 have not been fruitful, as these motifs are present at a very dynamic domain of the protein (CRD). Hence, attempts to identify unique motifs representing each structure have not been fruitful.

1. Cholesterol interactions, distributions and modulations could give valuable insight into their influence on the activation mechanism. As cholesterol is present in the simulations, this data could be easily screened for cholesterol receptor interactions throughout the activation pathway.

The response to this question has already been made a part of the response to 'Revisions essential for endorsement' point 2.

1. Experimental structures have already revealed the conformational changes between inactive and active SMO, in particular, the shift of TM6 and the movement of W535. This should be clarified in the text and interpreted in light of the new results.

We thank the reviewer for this comment. The text has been modified in the manuscript to reflect the suggested changes.

Modified Text: Introduction:

"Mutagenesis studies have outlined the presence of an intracellular W7.55𝑓 -R6.32𝑓𝜋-cation lock(40) in Class F that is broken on activation (Fig. 1A)"

Modified Text: Results, SMO activation involves a conserved molecular switch:

"M4496.30𝑓's outward movement is a proxy for the outward movement of TM6 a process associated with canonical GPCR activation(33, 38)"

1. While the authors calculated the mean first passage times during the apo simulation, they did not correlate this to the presence and absence of agonists. This could give further insight into how those modulators are influencing the activation pathway.

The mean first passage times could not be calculated in the presence of agonists, as the different intermediate states observed during apo-simulation (I1-3) were not observed during the agonist-bound simulations. Hence, we can say that the presence of the agonist locks the protein in an active state, unable to be explored using unbiased MD-simulations.

1. [Methods]: The used analysis scripts could be deposited/made available (e.g. how the Chapman-Kolmogorov test was implemented).

We appreciate the reviewer's request for the scripts. The scripts have been uploaded to github.

1. The study would have a greater influence on the field by further investigations on the agreement between simulations and experiments.

We agree. Experimental validation will play a key role in further uncovering and verifying the claims made in this manuscript. As a guide to experimentalists, wherever possible, we have added suggested mutations for further verifying the computational study.

(This is a response to peer review conducted by Biophysics Colab on version 1 of this preprint.)

Endorsement statement (22 December 2022)

The preprint by Suarez-Delgado et al. explores the mechanisms by which the Hv1 voltage-activated proton channel is dependent upon transmembrane voltage and pH by incorporating the small fluorescent non-canonical amino acid Anap into the S4 helix and monitoring its fluorescence. Anap spectra suggest the fluorophore resides in an aqueous environment and moves relative to a quenching aromatic residue (F150) in the S2 helix upon depolarization. Two kinetically distinct components of fluorescence change support the presence of at least three conformational states in the activation pathway of Hv1. Measurements using different pH gradients suggest that S4 movement and channel opening are similarly affected by pH gradients. This is the first study to incorporate Anap into Hv1, and provide a rigorous and thorough characterization of how the fluorophore can be used to explore mechanisms of gating and regulation, paving the way for future studies. The work will be of interest to physiologists and biophysicists investigating membrane protein mechanisms using non-canonical fluorescent amino acids.

(This endorsement by Biophysics Colab refers to version 2 of this preprint, which has been revised in response to peer review of version 1.)

Endorsement statement (6 December 2022)

The preprint by Yang et al. asks how the shape of the membrane influences the localization of mechanosensitive Piezo channels. The authors use a creative approach involving methods that distort the plasma membrane by generating blebs and artificial filopodia. They convincingly show that curvature of the lipid environment influences Piezo1 localization, such that increased curvature causes channel depletion, and that application of the chemical modulator Yoda1 is sufficient to allow channels to enter filopodia. The study provides support for a provocative “flattening model” of Yoda1 action, and should inspire future studies by researchers interested in mechanosensitive channels and membrane curvature.

(This endorsement by Biophysics Colab refers to version 2 of this preprint, which has been revised in response to peer review of version 1.)

Authors' response (28 November 2022)

GENERAL ASSESSMENT

This interesting preprint by Suárez-Delgado et al. explores the mechanism by which activation of the Hv1 voltage-activated proton channel is dependent upon both the voltage and pH difference across the membrane. The authors are the first to incorporate the fluorescent unnatural amino acid, Anap, into the extracellular regions of the S4 helix of human Hv1 to monitor transitions of S4 upon changes in voltage or pH. The authors first checked that Anap is pH insensitive for practical use in Hv1, where changes in local pH are known to occur when the voltage sensor activates and the proton pore opens. Anap was incorporated at positions throughout the S3-S4 linker and the extracellular end of S4 (up to the 202nd residue) of hHv1 and some positions showed clear voltage-dependent changes in fluorescence intensity. The authors also obtained fluorescence spectra at different voltages and observed no spectral shifts, raising the possibility that voltage dependent changes in fluorescence intensity could primarily be due to fluorescence quenching. Upon mutation of F150, the Anap signal at the resting membrane voltage increased, suggesting dequenching upon removal of F150. The authors also discovered that the kinetics of Anap fluorescence upon membrane repolarization have two phases (rapid and slow) under certain pH conditions and that there is a pH-dependent negative shift of the conductance-voltage (G-V) relation compared with the fluorescence-voltage (F-V) relation in some mutants. The biphasic kinetics of the fluorescence decay upon repolarization were explained by modelling a slower transition of return from intermediate resting state to a resting state. The pH-dependent shift of the G-V relation from the F-V relation provides insight into mechanisms of ΔpH-dependent gating of Hv1, a longstanding enigma. Overall, the approaches are rigorous, the figures show important results, and this work paves the way for the use of Anap fluorescence to study Hv1 gating and modulation.

We thank the reviewers for the careful reading and assessment of our manuscript and for the constructive criticism. We have tried to respond to all the essential revisions, both by rewriting sections and performing some experiments or new analysis. Below we respond one by one to all the points raised. Please also note that we have added an author to the manuscript, who has carried out new experiments included in this revised version of the preprint.

RECOMMENDATIONS

Revisions essential for endorsement:

1) In its current form, the narrative of the preprint has two threads. One on the mechanisms of Anap fluorescence changes (mainly quenching) and another on a previously unappreciated transition of the voltage sensor, as revealed by Anap. Our impression is that the preprint suffers somewhat from this split focus, which could be resolved by explaining why Anap was used to explore voltage sensor activation in Hv1 in the introduction. Perhaps the authors could also explain the advantage of smaller sized fluorophores compared to other maleimide-based fluorophores earlier in the introduction, or the utility of being able to insert Anap into transmembrane segments. The authors should more clearly point out how they exploited the advantages of Anap as a tool in this study. It would furthermore be helpful to discuss previous studies using nongenetic tools for VCF and spell out how they have delineated key aspects of Hv1, which would help to emphasize how several positions studied here (for example, 201 and 202) could not be labelled with cysteine-based fluorophores.

We think that this is a very useful suggestion and we have expanded the introduction to more pointedly indicate the contributions of previous voltage-clamp fluorometry experiments in Hv1 channels and to clearly explain why we chose to pursue the use of a genetically-encoded small fluorophore such as Anap.

2) We think the authors should be cautious about understanding the physicochemical nature of Anap using prodan as a model. It would be helpful to discuss the possibility that undetected spectral shifts due to a nonquenching mechanism could be overlooked, even though major signal changes can be explained by fluorescence quenching in their data. Regarding the mechanisms of remaining voltage-dependent fluorescence changes of F150A-A197Anap, it would be helpful for the authors to suggest possible ideas about which residues might account for remaining signals.

The beautiful spectral data for Anap is impressive. However, the physicochemical basis of the fluorescence change of Anap cannot be understood by simple extension of findings for prodan, which shows structural similarity to Anap. Our understanding is that changes in Anap fluorescence can only reveal a change in the structural relationship between Anap and one of its neighbors because the physicochemical basis of Anap fluorescence is complicated. For example, fluorescence could also be affected by the electrostatic environment, stretch of peptide bond, etc. Previous studies, including those of TRP channels, showed that the kind of environmental changes that Anap faces in ion channels do not necessarily induce large spectral shifts, unlike in cell-free spectral analyses using distinct solvents. Further, only minor shifts in spectra occur upon local structural change, as seen in previous work including Xu et al. Nat. Commun. 2020 11:3790. Such minor shifts could be perhaps overlooked even when Anap is incorporated into S4 and exposed to environmental change. Therefore, it is not easy to decode the physicochemical basis of Anap fluorescence changes. F150A-A197Anap has increased fluorescence and no change in spectral pattern, leading the authors to conclude that F150 quenches Anap fluorescence of A197 position. However, a significant amount of fluorescence change still occurs upon changes in membrane potential after F150 is changed to alanine (Figure 4). It is very likely that quenching is not the only mechanism underlying the observed voltage induced change of Anap fluorescence of Hv1. The authors suggest that remaining voltage-dependent fluorescence change of F150A-A197Anap could be due to interaction with other aromatic residues, but this has not been tested.

Thank you for pointing out our oversimplified discussion of the mechanisms of Anap fluorescence changes in Hv1 channels. We have taken into account your comments and present a more nuanced and toned-down discussion of the possible mechanisms at play in our experimental system.

3) The current version of the preprint is missing important control experiments, ideally performed using western blots to measure protein expression or, if that is not possible, proton current and fluorescence measurements, to demonstrate that protein expression or functional channels are not seen for all mutants in the absence of ANAP (but in the presence of the tRNA and Rs construct). A similar control for imaging would be to use ANAP alone without encoding.

We thank the reviewers for this recommendation. We show that the number of cells showing mCherry fluorescence is greatly diminished in the absence of L-Anap, but in the presence of the tRNA and synthetase. As suggested, we have included results of control experiments in which we attempted to record currents from cells expressing the constructs: F150A-A197tag, Q191tag, A197tag and L201tag co-expressed with the tRNA and synthetase-coding plasmid (pANAP) and in the absence of L-Anap. We struggled to find red fluorescing cells and recorded currents from a relatively small number of these cells, most of which was leak current. We now include these data in Figure 1-Supplement 1B. These control experiments show that there is very little leakage of expression of channels that did not incorporate Anap.

4) Aromatics in the S4 segment were ruled out as potential quenchers on the assumption that they would move together with Anap during gating. It should be noted, however, that Hv1 is a dimer and therefore a fluorophore attached to S4 in one subunit could be quenched by S4 aromatics in the neighboring subunit if were close to the dimer interface. In Fujiwara et al. J. Gen. Physiol. 2014 143:377-386, for example, W207 does not appear very far from labeled positions in the adjacent S4. This possibility should be mentioned in the discussion.

We appreciate the reviewers' concern regarding the role of other aromatic residues near Anap incorporation sites, especially the ones close to the subunit interface given that Hv1 is a dimer. We now mention the possibility that other residues could be quenching groups, especially given the fact that some quenching remains in the double mutant F150A-A197Anap (line 272 in results and line 432 in discussion). We have also included a new analysis of the ratio of Anap/mCherry fluorescence (at resting membrane potential) for all insertion sites. This shows a decreased ratio as Anap gets inserted in residues closer to the c-terminus of S4, which is evidence of a quenching group located near the center of the transmembrane domains (Figure 4-Supplement 1).

5) It is not clear whether the Anap spectra purely represent Hv1 incorporated into the plasma membrane or perhaps include signals from the cytoplasm or channels in internal membranes (whether assembled or incompletely assembled). It would be helpful to provide a more complete presentation of the data obtained and to provide more information in the Methods Section. In the Methods section, it is stated "The spectra of both fluorophores (Anap and mCherry) were recorded by measuring line scans of the spectral image of the cell membrane, and the background fluorescence from a region of the image without cells was subtracted". How are signals from cell membranes specified in this method being discriminated from those associated with the cytoplasm and intracellular membranes? If spectral data include signals from free Anap in the cytoplasm or Hv1 in intracellular membranes, spectral shifts upon membrane potential changes will be difficult to detect, even when Anap is incorporated into Hv1 and senses environmental change by voltage-induced conformational change. In Figure 3E, wavelength spectra were shown as standardized signals for different voltages. Amplitude change would be demonstrated (spectrum at different voltages without standardization should be shown).

We appreciate the concern related to the origin of the fluorescence signals and we have improved both the presentation and the associated figures. Since this is also a concern for the experiments that determined the pH-dependence of Anap incorporated at position Q191, we have included a figure supplement 1 to Figure 2 in which we explain how the membrane was visualized. We use mCherry fluoresce as an indication of plasma membrane-associated channels, since its red fluorescence is easier to detect in the membrane than Anap fluorescence (even though cytoplasm dialysis in whole-cell should diminish the amount of free Anap, it is difficult to distinguish Anap fluorescence in the membrane by itself). Once the membrane associated mCherry fluorescence is detected, the measurement of the spectrum from a very small membrane area is insured because the spectrograph slit delimits light collection to a very small vertical area and the horizontal line scan further limits light measurement. These procedures are now made explicit in methods section and supplementary figure mentioned before. Moreover, we explain that they were also followed in experiments where the cell was under voltage-clamp. The spectral data in Figure 3E is now presented without normalization to show the voltage-dependent change in amplitude without changes in peak emission wavelength.

In Figure 4, spectra were compared between A197Anap and F150A-A197Anap, showing increases of fluorescence in F150A-A197Anap. Was this signal measured at resting membrane potential? How does the spectrum change when the membrane potential is changed?

As in the experiments of figure 1E, the spectra were obtained in non-patched cells. Thus, the signal was measured at the HEK cell resting potential (~ -30 mV) and a ΔpH ≈ 0.2. We have now incorporated that information in the methods section and the figure description. On the other hand, we did not perform experiments measuring the double mutant spectra at different voltage steps, so we cannot respond to the second question.

Rationales for the confirmation of signals originating from the cell surface for Hv1 Anap might include the observations that: a) some mutants showed slightly different spectral patterns (in particular, Q191Anap showed a small hump at longer wavelengths, which is proposed to represent FRET between mCherry and Anap) and b) signal intensity was voltage dependent (if signals originate from endomembranes, they should not be voltage dependent). Mentioning these two points earlier in the text might help to alleviate concerns about the location of the protein that contributes to the measured signals.

These are great suggestions and we have incorporated them to the text (lines 156, 190 and 216 Results section), along with a better explanation of procedures followed to measure mostly membrane-associated fluorescence (see new Figure 2-Supplement 1).

6) In Fig 5, the fluorescence kinetics do not really match the current activation kinetics for panels A, B, and C. Is there an explanation for this mismatch? It would be helpful to have the fitted data in the figure. A more thorough comparison of the kinetics of currents and fluorescence would be helpful throughout the study.

We believe that the kinetics of fluorescence and current does not match because the current activation rate is overestimated due to a small amount of proton depletion present in recordings from large currents. This is an unavoidable problem in proton current recordings, even with the high concentration of proton buffer used in our experiments and the long time-intervals between each voltage pulse. For this reason, we did not undertake a systematic exploration of kinetics. Nonetheless, the current and fluorescence rates are very close and have the same voltage dependence, indicating a close correlation between voltage-sensor movement and current activation. We now explain this limitation in the manuscript text (line 223 and 327, results section).

7) Which construct of hHv1 was used to obtain the data in Figure 6? Unless we missed it, this information is not provided in the text or figure legend. Is it for L201Anap? This figure also shows an intriguing finding that the G-V relationship is negatively shifted from the F-V relationship at pHo7-pHi7 but not at pHo5.5-pHi5.5. A shifted G-V relation with the same ΔpH contrasts with what has been reported in other papers. However, the authors did not really discuss this surprising finding in the light of previous references. Could the shift of the G-V relation between two pH conditions with the same ΔpH be due to any position-specific effect of Anap? If Figure 6 represents L201Anap mutant, the presence of Anap at L201 probably makes such shift of G-V curve in Figure 6C? The authors should openly discuss this finding in relation to what has been reported in the literature.

Yes, construct L201Anap was used in Figure 6. This is stated now in the figure legend and in the corresponding main text. We agree that the leftward shift of the GV with respect to the FV in pHi7-pHo7 is an intriguing finding, suggesting that coupling between S4 movement and proton permeation can be regulated by the absolute value of the pH. We discuss this in the results section. The DeCoursey group has shown evidence in W207 mutants of hHv1 that the absolute value of pH can modulate the voltage dependence of the conductance. Although we had mentioned these results, we now mention them more prominently and also discuss the possibility that this might be a unique feature of introducing Anap at L201.

8) The authors suggest that the small hump near 600 nm in Figure 1E represents FRET between Anap and mCherry. It is surprising that FRET can take place across the membrane. Can the authors point to another case of FRET taking place across a cell membrane? One possibility might be that misfolded proteins place mCherry and Anap close to each other. It is also curious that only A191Anap did not show such a FRET-like signal. Also, if there is FRET, why wouldn't this also contribute to the voltage-dependent changes in fluorescence?

We thank the reviewers for bringing up this point. Based on published data, we assumed that mCherry could not be excited by 405 nm radiation, thus our conclusion that the observed emission near 604 nm is FRET between Anap and mCherry. We have now measured the excitation of the Hv1-mCherry construct and observe that the 405 nm laser is capable of exciting mCherry and produced ~2 % emission (as compared to 514 nm excitation), which is almost the same as that observed for the Hv1Anap-mCherry channels. We now conclude that the second hump in the emission spectrum near 600 nm is due to direct excitation of mCherry.

On the other hand, FRET across the membrane has been demonstrated for the membrane-bound hydrophobic anion dipicrylamine and membrane-anchored GFP (Chanda, et al. A hybrid approach to measuring electrical activity in genetically specified neurons. Nature neuroscience, 2005, vol. 8, no 11, p. 1619-1626.) and dipicrylamine and GFP in the c-terminus of CNG channels (Taraska & Zagotta, Structural dynamics in the gating ring of cyclic nucleotide–gated ion channels. Nature structural & molecular biology, 2007, vol. 14, no 9, p. 854). Finally, single-molecule FRET between dyes placed extracellularly and intracellularly in Hv1 channels has been demonstrated (Han et al. eLife 2022;11:e73093. DOI: https:// doi. org/ 10. 7554/ eLife. 73093).

A191Anap shows the hump at ~600 nm, but we think it's less evident because Anap at 191 is less quenched (see Figure 4-Supplement 1 and answer to point 4 above).

9) F150A-A197Anap shows a leftward shift of the F-V relation compared with the G-V relation only when ΔpH=1. Another unusual finding with F150A-A197Anap is the very small shift of the G-V relation between ΔpH=0 and ΔpH=1, when other reports in the literature suggest it should be 40 mV or more. Are these peculiar properties simply due to the absence of Phe at position 150, which might play a critical role in gating as one of the hydrophobic plugs of Hv1? To address this possibility, it would be ideal to compare different ΔpH values with and without F150 when Anap is incorporated at a different position (such as L201Anap). Regardless, it would be helpful to discuss this point.

We now discuss these changes in the discussion (lines 440-446).

10) In Figure 1E, I202Anap exhibits a blue shift in its spectrum suggesting the environment of Anap on I202 is more hydrophobic than the other sites. We presume these spectra were obtained at a negative membrane voltage, but the text or legend should clearly state how these were obtained. The authors should also explain whether the whole cell or edge was imaged. If these are at negative membrane voltages, might the Anap spectrum shift to higher wavelengths (i.e. more hydrophilic) when the membrane is depolarized? Did the authors find any spectral shift for I202Anap when doing a similar test as depicted in Figure 3E?

Yes, the spectrum of I202Anap was obtained at the resting potential (~ -30 mV), as were all spectra in Figure 1E. We now indicate this clearly in the methods section and in the figure legend. Fluorescence was measured from the membrane region as indicated by mCherry fluorescence and as illustrated in Figure 2-Supplement 1. We did not explore this mutant further and we cannot answer the question of whether a depolarizing potential might produce a red shift of the spectrum.

11) In Figure 3E, spectra are shown as normalized signals for different voltages, but an amplitude change should also be demonstrated by providing raw spectra at different voltages.

We have changed figure 3E to show non-normalized data that now show the increase in fluorescence intensity and no wavelength shift in the fluorescence spectrum of Anap (see also response to point 5).

12) In Figure 4, spectra are compared between A197Anap and F150A-A197Anap, showing increase of fluorescence in F150A-A197Anap. Were these obtained at a negative membrane voltage? How do these spectra change when membrane potential is changed?

See response to point 4 of "Revisions essential for endorsement" section.

Additional suggestions for the authors to consider:

1) The authors propose that Anap fluorescence tracks an S4 movement involved in the opening of the channel. They also argue that the existence of more than one open state could explain why the increase in florescence upon depolarization lags the proton current in most cases. While they convincingly show that Anap is not pH sensitive per se, when incorporated into the protein, the fluorescence efficiency of the fluorophore could still be affected by protonation of channel residues in the immediate environment when the channel opens, even after S4 has completed its movement. To address this alternative explanation, the authors could use Hv1 mutants with strongly reduced proton conductance. Channels bearing mutations corresponding to N214R or D112N were used successfully to isolate Hv1 gating currents from the much larger proton currents (De La Rosa & Ramsey, Biophys. J. 2018 114:2844-2854; Carmona et al. PNAS 2018 115:9240-9245; Carmona et al. PNAS 2021 118: e2025556118). Perhaps, they could be used with patch clamp fluorometry as well?

This is an interesting suggestion that could be explored in a follow up study.

2) The data showing that Hv1-197Anap is quenched by Phe at position 150 are very nice. Yet, it would be useful to show that the quenching is specific to F150 using a negative control. F149, for instance, is just next to F150 but points in a different direction, so its mutation to alanine should not affect Hv1-197Anap fluorescence.

This is an interesting suggestion, but, as suggested by reviewers, we think there is a possibility that other aromatic residues could contribute to quenching. Given the absence of a reliable structure for Hv1, prediction of the relative positions of any resides is very difficult and thus we did not attempt the suggested experiment.

3) A major finding of this work is the identification of a slow kinetic component that is highly sensitive to ΔpH. Earlier studies found that the ability of Hv1 to sense ΔpH is altered by some channel modifications, e.g., in the loop between TMH2 and TMH3 (Cherny et al. J. Gen. Physiol. 2018 150:851-862). Did the authors check whether any of these modifications alter the transition responsible for the slow kinetic component? For instance, a suppression of the transition resulting from a H168X mutation would help tighten the link to ΔpH sensing.

We did not carry out any of these experiments.

4) We understand that it is difficult to tightly control intracellular and extracellular pH when Hv1 is heterologously expressed in mammalian cells. The G-V relation is not always reliable because accumulation of protons or depletion of protons upon Hv channel activity will alter gating, as the authors have previously published (De La Rosa et al., J. Gen. Physiol. 2016 147:127-136). Could the kinetic analysis of Anap fluorescence be affected by similar alterations to proton concentration in the vicinity of Hv1? It would be helpful for the authors to comment on this specifically.

Thanks for this suggestion. Yes, we think that the kinetics, specially of ionic currents can be affected by even small changes in the pH gradient, for this reason we did not attempt a systematic kinetic analysis. We mention this in the text where we compare the voltage dependence of current and fluorescence activation for construct A197Anap (line 223).

5) Quenching of Anap by Phe could be verified in cell free conditions using a spectrophotometer with different concentrations of Phe, or citing the literature if it has already been reported.

We attempted this experiment but were unsuccessful in observing Anap quenching by phenylalanine at the concentrations of phenylalanine that can be attained in aqueous solution. We suspect that Phe quenching of Anap could happen by electron transfer or ground-state complex formation, in which case near proximity is necessary and higher concentrations of Phe would be required to detect quenching in solution. However, we measured the absorbance of Anap in the absence and presence of phenylalanine (Phe) (and tyrosine (Tyr)) at the concentrations that can be achieved in aqueous solution (8 mM and 1mM, respectively). Absorbance measurements can detect ground-state complex formation even at relatively low concentrations (J.R. Lakowicz, 1999, Principles of Fluorescence Spectroscopy). We observed that the absorbance of Anap is modified by the presence of Tyr or Phe, indicating that these amino acids indeed interact with Anap, possibly through ground-state complex formation. We include this data for the reviewers to inspect.

6) The authors did not cite any example of Anap incorporation into S4 helices, but there are several recent papers where Anap was utilized to probe motion of S4 in other channels. Examples include Dai et al., Nat. Commun. 2021 12:2802 and Mizutani et al. PNAS 2022 119:e2200364119.

Thanks for this observation, we have included these important results in the discussion.

7) In the Anap-free negative control (with only A197TAG plasmid transfection), the mCherry signal seems positive (Supplementary Figure 1, left row, second from the top). Is this due to unexpected skipping of the TAG codon to make mCherry-containing partial polypeptides? It would seem like an explanation is needed.

Thanks for bringing this up. We do not know the exact origin of these leak expression of red fluorescence. We think that, as suggested, there is a possibility that skipping of the Amber codon can lead to a methionine at the end of S4 acting as a second translation initiation site, giving rise to truncated channels that would express mCherry but not currents. This is consistent with the fact that we cannot detect currents in the absence of Anap but we see a small number of red cells.

8) The data of Figure 3E are shown as data with different membrane voltages. But there is no information about membrane voltage for Fig. 1E and Fig. 2A and Fig. 4B. Are these from unpatched cells? Please clarify.

See response to point 4 of "Revisions essential for endorsement" section.

9) G-V relations are shown for F150A-A197Anap, but current traces of F150A-A197Anap are missing.

We have modified the figure to include current and fluorescence traces.

10) On Page 11, Line 303 says "experimental F-V relationship is positively shifted by 10 mV with respect to the G-V curve". But looking at the data Fig5D, the shift at ΔpH=2 seems the opposite. Perhaps "positively" should be "negatively" in this sentence?

Thanks for pointing out this mistake. We have found that this misunderstanding was provoked because of a mistake with the image labeling of F-V and G-V curves for the ΔpH=2 data, we have now corrected the figure. The shift of F-V is indeed positive to G-V as stated before.

(This is a response to peer review conducted by Biophysics Colab on version 1 of this preprint.)

Endorsement statement (17 November 2022)

The preprint by Atsumi et al. describes how chloride binding to sweet- and umami-sensing proteins (T1R taste receptors) can evoke taste sensation. The authors use an elegant combination of structural, biophysical and electrophysiological approaches to locate a chloride binding site in the ligand-binding domain of medaka fish T1r2a/3 receptors. They convincingly show that low mM concentrations of chloride induce conformational changes and, using single fiber recordings, establish that mouse chorda tympani nerves are activated by chloride in a T1R-dependent manner. This suggests that chloride binding to sweet receptors could mediate the commonly reported sweet taste sensation following ingestion of low concentrations of table salt. The findings will be of broad relevance to those studying taste sensation and ligand recognition in GPCRs.

(This endorsement by Biophysics Colab refers to version 2 of this preprint, which has been revised in response to peer review of version 1.)

Authors’ response (5 November 2022)

GENERAL ASSESSMENT

Piezo1 and Piezo2 are stretch-gated ion channels that are critically important in a wide range of physiological processes, including vascular development, touch sensation and wound repair. These remarkably large molecules span the plasma membrane almost 40 times. Cryo-EM and reconstitution experiments have shown that Piezos adopt a cup-like structure and, by doing so, curve the local membrane in which they are embedded. Importantly, membrane tension is a key mediator of Piezo function and gating, an idea well-supported several independent studies. Cells have varied three-dimensional shapes and are dynamic assemblies surrounded by plasma membranes with complex topologies and biochemical landscapes. How these microenvironments influence mechanosensation and Piezo function are unknown.

The current preprint by Zheng Shi and colleagues asks how the shape of the membrane influences Piezo location. The authors use creative approach involving methods to distort the plasma membrane by generating “blebs” and artificial “filopodia”. Overall, the work convincingly shows that the curvature of the lipid environment influences Piezo localization. Specifically, they show that Piezo1 molecules are excluded from filopodia and other highly curved membranes. These experiments are well controlled and the results fully consistent with previous structural and biochemical work. Furthermore, the work explores the hypothesis that a chemical modulator of Piezo1 channels called Yoda1 functions by “flattening” the channels, a movement previously proposed to be linked to mechanical gating. Consistent with this model, the authors show that Yoda1 application is sufficient to allow Piezo1 channels to enter filopodia. While the flattening model is provocative hypothesis, hard evidence awaits structural verification.

Overall, the preprint by Shi and colleagues will be of interest to scientists studying how mechanical forces are detected at the molecular level. The work introduces important concepts regarding how the shape of cellular membranes affects the movement and function of proteins within it. The technical advance for changing the shape of a plasma membrane is of note. 

We thank the reviewers for the accurate summary and positive assessments of our manuscript. We address each of the concerns below.

RECOMMENDATIONS

Revisions essential for endorsement:

As is evident from the comments below, our endorsement of the study is not dependent on additional experiments. However, we feel more experimental clarification is needed, that providing clearer images would be helpful, and, most importantly, we would like alternative conclusions and caveats to be mentioned.

1. Can the authors comment on the link between the conclusions that (1) the presence of filopodia prohibits Piezo1 localization (Fig 1) and (2) Piezo1 expression prohibits the formation of filopodia (Fig 3). As it stands, it is hard to understand if there is a cause and effect relationship here or if these are separate, unrelated observations? We recommend revising the discussion to clarify.

We now clarify the link between Piezo1’s curvature sensing (depletion from filopodia) and its inhibition effect on filopodia formation before presenting the current Fig. 5: “Curvature sensing proteins often have a modulating effect on membrane geometry. For example, N-BAR proteins, which strongly enrich to positive membrane curvature, can mechanically promote endocytosis by making it easier to form membrane invaginations (Shi and Baumgart, 2015; Sorre et al., 2012). Thus, we hypothesize that Piezo1, which strongly depletes from negative membrane curvature (Fig. 1, Fig. 2), can have an inhibitory effect on the formation of membrane protrusions such as filopodia.”

2. When comparing the images of Fig. 2A, B to those of Fig. 2C, D, it appears that bleb formation induces a drastic enrichment of Piezo1 in the bleb membrane. Is this due to low membrane tension in the bleb? If this is the case, it indicates that the level of membrane tension has a prominent role in determining the localization of Piezo1.

We apologize for this confusion due to our poor wording and figure presentation in the manuscript. By “Piezo1 clearly locates to bleb membranes” we didn’t mean to indicate that Piezo1 is enriched on bleb membranes as compared to the cell body. Rather, we meant to emphasize Piezo1’s localization to the *membrane* of the blebs rather than in the cytosolic space.

Cells in 2C, 2D are different from that in 2A and 2B and were presented with different image contrasts. We now include the images of the full cell for Fig. 2C and 2D as the current Figure S8. To focus on the equator of the bleb, the cell body was out of focus. However, there is no indication that Piezo1 density is significantly different between the bleb membrane and the intact parts of the plasma membrane.

We changed the main text to: “Similar to previous reports (Cox et al., 2016), bleb membranes clearly contain Piezo1 signal, but not significantly enriched relative to the cell body (Fig. 2C, 2D; Fig. S8).”

In line with this, it appears more Piezo1 proteins are localized in less tensed tethers. Thus, might your observations be equally consistent with tension rather than curvature as a key regulator of Piezo1 localization? We recommend adding this to your discussion.

We now explain the deconvolution between tension and curvature effects in detail. We also performed additional experiments to quantify the membrane tension in cells and blebs (current Fig. S9).

In the Results section, we add: “Tethers are typically imaged > 1 min after pulling, whereas membrane tension equilibrates within 1 s across cellular scale free membranes (e.g., bleb, tether) (Shi et al., 2018). Therefore, the sorting of Piezo1 within individual tension-equilibrated tether-bleb systems (Fig. 2C – 2G) suggests that membrane curvature can directly modulate Piezo1 distribution beyond potential confounding tension effects.”

In the Discussion section, we add: “In addition to membrane curvature, tension in the membrane may affect the subcellular distribution of Piezo1 (Dumitru et al., 2021). Particularly, membrane tension can activate the channel and potentially change Piezo1’s nano-geometries. This tension effect is unlikely to play a significant role in our interpretation of the curvature sorting of Piezo1 (Fig .2): (1) HeLa cell membrane tension as probed by short tethers (Fig. S9F; 45 ± 29 pN/ µm on blebs and 270 ± 29 pN/ µm on cells, with the highest recorded tension at 426 pN/ µm) are significantly lower than the activation tension for Piezo1 (> 1000 pN/µm (Cox et al., 2016; Lewis and Grandl, 2015; Shi et al., 2018; Syeda et al., 2016)). (2) With more activated (and potentially flatten) channels under high membrane tension, one would expect a higher density of Piezo1 on tethers pulled from tenser blebs. This is the opposite to our observations in Fig. 2C - 2G, where Piezo1 density on tethers was found to decrease with the absolute curvature, thus tension (eq. S6), of membrane tethers.”

3. Given the intrinsically curved structure of Piezo1, it is difficult to understand the model’s prediction that curved Piezo1 is not enriched in 25-75 nm invaginations. Where will Piezo1 normally reside in the plasma membrane? It would be helpful if this could be discussed.

The spontaneous curvature from our model _C_0 (_C_0-1 = 83 ± 17 nm, the value is updated after refitting to more data points collected for Fig. 2G) represents a balance between the intrinsic curvature of Piezo1 trimers (0.04 ~ 0.2 nm-1 as suggested by CryoEM studies(Haselwandter et al., 2022; Lin et al., 2019; Yang et al., 2022)) and that of the associated membrane (0 nm-1, assuming lipid bilayers alone do not have an intrinsic curvature). We now refer to _C_0 as the “spontaneous curvature of the Piezo1-membrane complex” throughout the manuscript, rather than the “spontaneous curvature of Piezo1”.

Our model, when extrapolated to membrane invaginations, predicts a weak enrichment of Piezo1 on ~100 nm invaginations (peak at 83 nm), but a depletion of Piezo1 on more highly curved invaginations. This is simply because it would be energetically costly to fit a protein-membrane complex to a curvature that is different from what the complex prefers (in the case of 25-75 nm membrane invaginations, the membrane curvature would be too high for the Piezo1-memrbane complex).

However, it is worth pointing out that Piezo1-membrane complex may not present the same spontaneous curvature on positively and negatively curved membranes. More importantly, we do not yet have direct evidence to show that this depletion indeed happens in the exact range of invagination curvature we predicted. We now acknowledge this limitation in the Discussion section: “However, it is worth noting that we assumed a zero spontaneous curvature for membranes associated with Piezo1 and that the spontaneous curvature of Piezo1-membrane complex is independent of the shape of surrounding membranes. These assumptions may no longer hold when studying Piezo1 in highly curved invaginations or liposomes (Lin et al., 2019).”

We also took this opportunity to verify the key prediction from the extrapolated model - that Piezo1 would enrich towards ~ 100 nm radius cell membrane invaginations. To achieve this, we utilized a recent development in nanotechnology, pioneered by Wenting Zhao and Bianxiao Cui’s labs (Lou et al., 2019; Zhao et al., 2017). An illustration of the experimental design and detailed findings are summarized in the current Fig. 3 and briefly discussed below.

In collaboration with Wenting Zhao’s lab, we cultured cells on precisely engineered nanobars with curved ends and flat central regions. For a labelled membrane protein of interest, the end-to-center fluorescence ratio would report the protein’s curvature sorting ability. We find that Piezo1 enriches to the curved ends of nanobars, whereas membrane marker signals are homogeneous across the entire nanobar (Fig. 3). The finding achieved strong statistical significance via hundreds of repeats on nanobars of the exact same geometry, a major technical strength of our chosen system. Furthermore, the enrichment of Piezo1 was observed on nanobars with 3 different curvatures (corresponding to diffraction-limited radii between 100 to 200 nm) and qualitatively agrees with our model (current Fig. S10). While further investigations on a wider range of membrane curvature are required to fully map out the sorting of Piezo1 on membrane invaginations, our data in the current Fig. 3 clearly verifies the prediction that membrane curvature can lead to enrichment of Piezo1 on cellular invaginations.  

We now refer to this new finding in the Abstract, along with the previously observed depletion of Piezo1 on filopodia. We present a detailed description of the experiment and associated findings in the Results and the Method sections.

4. It is currently unknown whether and how long Yoda1 might keep Piezo1 in a flattened state. Given that Yoda1 is highly hydrophobic, it might affect membrane properties instead of the curvature of Piezo1. These caveats should be discussed.

We thank the reviewers for pointing out the potential effect of Yoda1. We did additional experiments to confirm that on Piezo1-KO cells, Yoda1 molecules alone do not significantly alter the formation of filopodia, in contrast to observations in WT cells. This data suggests Yoda1 (at the concentration we use) is unlikely to significantly alter the mechanical properties of the plasma membrane. The data is now presented as Fig. 5E in the updated manuscript. We added: “In Piezo1 knockout (Piezo1-KO) cells, adding Yoda1 to the culture medium does not significantly change the number of filopodia (Fig. 5E), suggesting the agonist does not directly regulate filopodia formation without acting on Piezo1.”

5. The authors state that “Yoda1 leads to a Ca2+ independent increase of Piezo1 on tethers”. It has not been determined yet that Yoda1 leads to Piezo1 flattening (or even opening). In Electrophysiology experiments, unless there is pressure applied, Yoda1 does not lead to substantial currents. Therefore, the cartoon of Yoda1 flattening Piezo1(3H) is misleading. We recommend revising this. So far, the best experimental evidence on flattening is via purified channels reconstituted in various sizes of liposomes. However, it is plausible that the flattened shape is closed or open inactivated. Because most of the claims of this paper depend on the curved vs flattened shape of Piezo1, the authors should address these caveats carefully.

We thank the reviewers for pointing out the limitations in our current understanding of Yoda1. We agree that our data do not directly show the flattening of Piezo1 by Yoda1, rather it is consistent with the flattening hypotheses. We lowered the tone of our conclusion to Fig. 4 to: “Our study suggests this conformational change of Piezo1 may also happen in live cells (Fig. 4H).” We also added arrows in Fig. 4H to suggest that membrane tension helps the proposed flattening of Piezo1 by Yoda1.

We think our experiment may also provide new insights on the action of Yoda1: First, we note that only a small fraction of filopodia responded to Yoda1, and pre-stressing of the cell membrane was required to amplify the Yoda1 effect (current Fig. 4E). This observation is consistent with the reviewers’ notion that membrane tension is likely required to flatten Piezo1, even in the presence of Yoda1. Secondly, highly curved liposome or detergents can confine the shape of Piezo1 trimers. Therefore, the inability to observe Yoda1-induced flattening of Piezo1 in small liposomes is not necessarily in contradiction with our observation in the mostly flat cell membranes.

We add to the Discussion section: “Yoda1 induced flattening of Piezo1 has not been directly observed via CryoEM. Our results (Fig. 4) point to two challenges in determining this potential structural change: (1) Yoda1 induced changes in Piezo1 sorting is greatly amplified after pre-stretching the membrane (Fig. 4E), pointing to the possibility that a significant tension in the membrane is required for the flattening of Yoda1-bound Piezo1. (2) Piezo1 is often incorporated in small (< 20 nm radius) liposomes for CryoEM studies. The shape of liposomes can confine the nano-geometry of Piezo1 (Lin et al., 2019; Yang et al., 2022), rendering it significantly more challenging to respond to potential Yoda1 effects. This potential effect of membrane curvature on the activation of Piezo1 would be an interesting direction for future studies.”

6. Page 9: "Our study shows this conformational change of Piezo1 in live cells (Fig. 3H)." We recommend that this claim be removed as it seems too strong for the provided data.

We changed the sentence to: “Our study suggests this conformational change of Piezo1 may also happen in live cells (Fig. 4H).”

Additional suggestions for the authors to consider:

1. Based on the calculated spontaneous curvature of Piezo1-membrane C0 of 87 nm, is it possible to derive the curvature of Piezo1 protein itself and the associated membrane footprint? This would be a nice addition.

It is possible to do such an estimation, however, many (unverified) assumptions must be made, in addition to the ones already in our model. First, we need to assume a size of the Piezo1 trimers and of the Piezo1-membrane complex. If we assume Piezo1 trimers are ~170 nm2 in the plane of lipid bilayers (based on estimates from PDB) and that the complex takes on the shape of a 10 -20 nm radius half-sphere. Effectively, Piezo1 occupies an area fraction of 6.7%~27% in the Piezo1-membrane complex. Next, we assume that the membrane and the Piezo1 trimer have the same bending rigidity. Finally, we assume that the membrane itself does not have an intrinsic curvature.

With those assumptions, the intrinsic curvature of Piezo1 trimers (_C_p) would relate to the spontaneous curvature of membrane-Piezo1 complex (_C_0) following: _C_p-1 = _C_0-1 * (6.7%~27%). Knowing _C_0-1 = 83 ± 17 nm, we get _C_p-1 = 5.6 nm ~ 22.4 nm.

2. It is hard to see the filopodia and their localization in the figures. It would be better for readers and more convincing if clearer/higher resolution example images could be provided.

We now provide high resolution figures.

3. Can the authors better explain how the calculations done in panel 1C and S3D are done and their importance?

Each fluorescence trace along the drawn yellow line was normalized to the mean intensity on the corresponding flat cell body, so that the average fluorescence of the cell body has a y-axis value of 1. We think the intensity traces are important because image contrast can be adjusted, therefore Fig. 1A alone would not convincingly show that there are no Piezo1 on filopodia.

4. In Figure 2E, are these data from hPiezo1 or mPiezo1? In other cases, hPiezo1 is specified, this this may be a typo?

Corrected.

5. Figure 3 F&G: We assume these cells are the same in all panels, just visualized with either mCherry or eGFP in each condition. Accordingly, we would have expected more swelling in hypotonic conditions, and wonder if further evaluation may resolve this apparent discrepancy? If not, please provide more clarification.

This is a good point. Indeed, we do observe a significant swelling of the cell right after the hypotonic shock.

However, this effect is expected to be transient (volume of the cell would recover after ~ 1 min), see Figure. 1C here: https://www.pnas.org/doi/10.1073/pnas.2103228118. Our images in Fig. 3F and 3G were taken ~10 min after the hypotonic shock.

6. On a lighter note, we’d recommend not using in cellulo.

We changed in cellulo to “in live cells”

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Syeda, R., Florendo, M.N., Cox, C.D., Kefauver, J.M., Santos, J.S., Martinac, B., and Patapoutian, A. (2016). Piezo1 channels are inherently mechanosensitive. Cell Reports 17, 1739-1746.

Yang, X., Lin, C., Chen, X., Li, S., Li, X., and Xiao, B. (2022). Structure deformation and curvature sensing of PIEZO1 in lipid membranes. Nature 1-7.

Zhao, W., Hanson, L., Lou, H., Akamatsu, M., Chowdary, P.D., Santoro, F., Marks, J.R., Grassart, A., Drubin, D.G., and Cui, Y. (2017). Nanoscale manipulation of membrane curvature for probing endocytosis in live cells. Nature Nanotechnology 12, 750-756.

(This is a response to peer review conducted by Biophysics Colab on version 1 of this preprint.)

Consolidated peer review report (4 November 2022)

GENERAL ASSESSMENT

Yang et al. present valuable insight about ligand interaction with SERT. It is notable for the use of endogenously expressed SERT from pig brain, rather than from a heterologous expression system, and the value of using Fab fragments as a tool for detecting and purifying SERT. The use of natively expressed SERT allows insight into binding sites for endogenous membrane components, including lipids, that copurify with the transporter. Data on binding of the psychostimulants methamphetamine and cocaine to the purified protein also adds to our knowledge of substrate and inhibitor interactions with SERT.

In general, we liked the manuscript but have some suggestions for improvement and clarification. There was unanimous agreement that the conclusions regarding SERT oligomerization were stated in a way that many readers would mis-interpret. Although the manuscript states that the result of the study do not exclude SERT oligomerization in its native environment, that statement is not reflected in the abstract and is downplayed in the discussion. The discussion clearly points out why some previous proposals for SERT oligomerization may conflict with our knowledge of SERT structure and function. However, it is also clear that the extraction of SERT using DDM, although it’s influence on SERT structure may be mild, can remove other membrane components that are required for oligomer stability.

A second issue raised by the reviewers concerns the poses of bound ligands and their effect on conformation. There is an expectation that substrate binding converts NSS transporters like SERT to a more inward-facing conformational ensemble while some inhibitors (particularly cocaine in the case of SERT) have the opposite effect. Statements in the manuscript that METH stabilizes an outward-open conformation while cocaine stabilizes an occluded state seem to contradict this expectation. A close reading of the results, and examination of the structures, indicates that the backbone of SERT is outward-open in both cases and that the orientation of Phe372 occludes cocaine but not METH. Thick and thin gates have already been defined for LeuT, so the implication that orientation of Phe372 represents an additional gating process may confuse readers.

The observation that METH does not stabilize a less-outward-open conformation may result from its lower affinity for SERT and one wonders why a more SERT-selective amphetamine derivative such as MDMA or p-chloroamphetamine was not used. Was the objective to compare the binding pose and conformational response of SERT to that of dDAT with the same ligands?

A third issue is the designation of SERT purified from pig brain as nSERT rather than “native porcine SERT” (pSERT or ssSERT for Sus scrofa). One wouldn’t use nSERT to define SERT extracted from Drosophila or C. Elegans by the same technique.

RECOMMENDATIONS

Revisions essential for endorsement:

1)     Clearly indicate that the lack of oligomer detection in detergent-solubilized SERT is not evidence against SERT oligomerization in situ, and that detergent can disrupt interactions required for oligomerization, thereby biasing the oligomeric status of SERT. Also, use an alternative for DDM-solubilized SERT other than “native” or “nSERT”

2)   Distinguish between the local occlusion of cocaine by reorientation of the Phe-372 side chain and the occluded conformational state of SERT that involves movement of TMs 1 and 6 towards TMs 8 and 10. Also explain the choice of METH rather than an amphetamine derivative more selective for SERT. Do the structures explain the difference in METH affinity between SERT and dDAT?

3)   Because neither the DHA density nor the MD simulations provide an unambiguous identification of DHA, designation of this density as DHA should be clearly stated as provisional.

Additional suggestions for the authors to consider:

1)     Does DHA fulfill a functional role? The carboxyl group is close to Arg141, which can form an ion pair with Glu531 to close the extracellular pathway. Is there any indication that DHA could interfere with this process, and alter SERT activity?

2)   Is there sufficient purified material to perform a lipidomic analysis and to confirm the identity of DHA at the allosteric site?

3)   Would incubation of the membranes with METH or cocaine prior to detergent extraction affect the composition of associated lipids?

4)   PIP2 has been proposed to promote SERT association in vivo. Is it possible that PIP2 addition would change the oligomeric nature of DDM-extracted SERT?

5)   We suggest trying to polish the final particle stack of both data sets further. Have the authors tried to separately refine the 3D classes from Relion, and not to combine them? Alternatively, one could perform an additional round(s) of heterogenous refinement on the final particle stack, and a final nonuniform refinement. There seems to be an opportunity to improve the quality of maps by further polishing the particles.

REVIEWING TEAM

Reviewed by:

Moitrayee Bhattacharyya: Assistant Professor, Yale University, USA: membrane protein structure and function

Azadeh Shahsavar, Assistant Professor, University of Copenhagen, Denmark: structural biology of transporters

Steffen Sinning, Associate Professor, Aarhus University, Denmark: ligand binding and selectivity in monoamine transporters

Curated by:

Gary Rudnick, Professor, Yale University, USA

(This consolidated report is a result of peer review conducted by Biophysics Colab on version 1 of this preprint. Minor corrections and presentational issues have been omitted for brevity.)

Authors' response (18 October 2022)

GENERAL ASSESSMENT

The sweet and umami sensor proteins, taste receptors type 1 (T1Rs) are important GPCRs underlying taste sensation. In humans, amino acids bind and activate the T1r1/3 heterodimeric receptors leading to umami taste perception, whereas sugars activate the T1r2/3 receptors leading to sweet taste perception. In this manuscript, Atsumi and colleagues combine structural, biophysical and electrophysiological methods to show that Cl- ions also bind to T1Rs, at low mM concentrations, to evoke taste sensation. The authors (1) identify a putative evolutionarily conserved Cl- binding site in the crystal structures of isolated LBDs from medaka fish T1r2a/3 receptors, (2) show that Cl- ions promote protein stability and induce conformational changes in these mfT1r2a/3 LBDs, independent of orthosteric ligands, and (3) demonstrate that mouse chorda tympani nerves are activated by Cl- ions via a T1R-specific mechanism. Based on these findings, the authors conclude that low concentrations of Cl- may bind to sweet receptors and mediate the commonly reported sweet taste sensation following ingestion of low concentrations of table salt.

The elucidation of the molecular mechanism(s) underlying salt taste sensation is a physiologically relevant question that will appeal to a broad audience. Moreover, the authors use an impressive array of different approaches to broadly cover numerous aspects, ranging from structural biology, to biophysics and physiological recordings. Overall, the identification of the chloride ion binding site is convincing, based on the previously solved structure, as well as the bromide ion substitution and long-wavelength Cl- anomalous difference analysis performed in this work. This analysis is supported by biophysical measurements showing that Cl- substantially stabilizes the wild type complex against thermal denaturation, but does not stabilize a point mutant in the putative Cl- binding site. The single fiber recordings suggest there is physiological relevance to the biophysical and structural findings, although they could be strengthened by additional control experiments. Overall, the possibility of Cl- ions acting as a sweet receptor ligand is enticing and the work will likely motivate additional research on this subject.

The authors appreciate the positive assessment of the study, as well as the valuable comments and suggestions from the reviewers described below. Considering the referees' remarks, we performed additional control experiments and obtained evidence strengthening the T1r-mediated chloride sensing, as described below.

RECOMMENDATIONS

Revisions essential for endorsement:

1. The authors should provide refinement statistics and methodology for both the Cl-- and Br-- bound structures, and some comparison between these two structures (global structural alignment & RMSD should be sufficient).

We used the X-ray diffraction data from the Br–-substituted crystal, as well as the long-wavelength data from the Cl–-bound crystal, to draw the anomalous difference-Fourier maps pinpointing the Br–/Cl– positions. The structure models used for phase calculation were obtained by molecular replacement as described in the "Crystallography" section in the Materials and Methods. To show the certainty of the molecular replacement solutions, we added the R-factors for the models in the last sentence of the section. Since the resolutions for these anomalous data were limited and the structural comparison between the Br–-bound and the Cl–-bound forms is not the main subject of the study, no further extensive structural refinement was performed on these data.

1. We would recommend that the authors perform nerve recordings using artificial saliva rather than water as the perfusate. This is a key point because the chloride concentration in saliva is approximately 15 mM. Thus, according to their binding data, most T1rs should have chloride bound at baseline. Perhaps this means that chloride binding is required to allow sucrose or other ligands to cause sufficient conformational changes and receptor activation? If this is the mechanism, it would still be quite interesting, but would change the framing/interpretation as presented in the manuscript. If additional experiments are not feasible, the authors should carefully discuss this point.

The authors thank the reviewers' insightful comments. We addressed this point and the results were shown in Figure 4D in the revised manuscript (Figure 3C in the original manuscript) and the third paragraph in the "Taste response to Cl– through T1rs in mouse" section in Results (p. 16, the next paragraph to the Figure 4 in the manuscript). As shown in Figure 4D, solely l-Gln or sucrose application in the absence of chloride (shown as l-Gln or sucrose) induced nerve responses. When those were applied in the presence of 10 mM chloride (shown as l-Gln+NMDG-Cl or sucrose+NMDG-Cl), the responses were increased to the similar levels as the summation of the response of the independent application of each substance. These results suggested that the chloride binding is not required for the receptor activation by sugars or amino acids, and that the binding of the two can occur simultaneously but does not cause synergistic responses.

1. Some of the conclusions would be strengthened by additional control experiments, especially for the data obtained using FSEC-TS (Fig. 2C) and single fibre recordings (Fig. 3). For instance, how specific is the T105A mutation in abolishing Cl‑-dependent conformational changes? Did the authors check how the T105A mutation affects the ability of the LBD to undergo conformational changes in response to (1) L-Gln only and (2) Cl- only? Have the authors tried running these experiments at lower Cl- concentrations? 304 mM Cl‑ (page 16, line 363) is much higher compared to the effective concentration range claimed by the authors. For the single fibre recordings, have the authors tried applying 10 mM NMDG-gluconate? Having this negative control will provide more confidence in the specificity of Cl--induced impulses. Also, we would recommend a demonstration of reversibility in the gurmarin effect shown in Fig 3A.

The authors thank the reviewers' important suggestions.

We performed a FRET assay for T1r2a/T1r3(T105A) mutant, and the results have been added to Figure 3E. In this experiment, we used 10 mM chloride, not ~300 mM, for both the T105A mutant and the wild-type LBD proteins and compared the results of the two. We confirmed that the extent of Cl–-dependent conformational change for the mutant was significantly reduced, as judged by the FRET index change. However, we also performed the same experiment using solely l-Gln as a titrant as the reviewers' suggested, and found that the amino acid-dependent change of the mutant was also significantly reduced. Therefore, although the former result itself agrees with our hypothesis, we are aware that the possibility of the entire protein deactivation during preparation cannot be excluded. Therefore, we presented the result with a notion about the study's limitations, as shown in the third paragraph in the section "Cl–-binding properties in T1r2a/T1r3LBD" in the Results (p. 12, the next paragraph to Table 1 in the manuscript).

Regarding the single fiber recordings, we performed the NMDG-gluconate application and confirmed that it did not induce significant responses at least up to 10 mM, as shown in Figure 4B. In addition, we described the method and results of our reversibility confirmation test for gurmarin inhibition in the section "Single fiber recording from mouse chorda tympani (CT) nerve" in Methods (the last paragraph of the section, p.25).

Additional suggestions for the authors to consider:

1. The introduction would benefit from greater focus and clarity to make the work more accessible to readers. Despite the overall focus on T1rs, only a quarter of the introduction revolves around these receptors. Additional information would help the reader to understand the research topic. For example, how many isoforms are there? Are these receptors obligate heterodimers? How similar are the mf T1r2a/3 compared to the human T1r2/3 receptors? If mf T1r2a/3 receptors are activated by amino acids, how useful a proxy are they in understanding sweet-sensing human T1r2/3 receptors? If T1r3 is found in both heterodimers, and amino acids bind to T1r3, how do these receptors discern between sweet and umami taste? What are the mechanisms underlying activation of these receptors? How are these receptors usually studied functionally?

We agree with the significance of the information pointed out by the reviewers, and several points are currently under investigation in the field. However, we decided to keep the current contents in the Introduction due to the length limitation imposed by the submitted journal.

1. Given the focus on isolated LBDs of (non-human) mfT1r2a/3 receptors, the authors are encouraged to comment on the probability of Cl- binding, and the subsequent conformational rearrangement observed in the isolated LBDs, actually translating to activation of (full-length) human receptors (and ultimately taste stimulation). Since the authors have previously assessed the function of hsT1r2/3 in HEK293 cells using Ca2+ imaging (PMID: 25029362), evaluation of the activation properties of Cl‑ at full-length receptors and testing the effects of T1r3 mutations on these Cl- effects would help to strengthen the manuscript. Also, there are several reported polymorphisms in the gnomAD database around the Cl- ion binding site (Thr102Met, Gly143Arg, Pro144Ser/Leu), so it would be interesting and helpful to test the effects of these variants that are found in the population. We do not expect the authors to perform these experiments, but in the absence of more conclusive functional data on full-length receptors, the authors should consider discussing these potential caveats in the text.

The authors thank the reviewers' suggestions. We attempted the Ca2+-imaging in the early stage of the study, but it failed due to the instability of the cellular responses under the Cl–-depleted conditions. In contrast, nerve recordings are durable under a wide range of conditions. We described the situation in the first paragraph in the section "Taste response to Cl– through T1rs in mouse" in the Results. To verify that the nerve responses were attributed to T1rs, we confirmed that the chloride-dependent responses were attenuated by gurmarin, a T1r-specific blocker, and in T1r3-knockout mice, which were added in the revised manuscript.

Furthermore, we additionally performed a mouse behavioral assay and confirmed the preference for the solution containing chloride relative to H2O, which was again abolished by gurmarin. The results supported our discussion that the chloride is detected through a taste signal transduction pathway mediated by T1rs, as described in the last paragraph of the same section, and shown in Figure 4E, F.

The authors thank the reviewers' interesting and thoughtful pointing about the polymorphism, which is worth to be addressed in future studies.

1. Given the availability of AlphaFold Multimer and the well-defined stoichiometry of the complex, did the authors attempt to predict a model of the full-length heterodimer? This may be informative with regards to the mechanism of signal transduction to the transmembrane domain.

The authors appreciate the reviewers' helpful suggestion. We have constructed the full-length heterodimer models of T1rs from several species. We hope we will utilize the knowledge derived from them in our future studies.

1. The nerve recording data would be more convincing if the authors could provide electrical recordings to truly sweet compounds at physiologically relevant concentrations (sucrose and artificial sweeteners). Currently, they only show data for 20 mM L-glutamine, which is not particularly sweet in Fig 3a-b, and then summary data for sucrose in Fig 3b.

The authors thank this comment. We added representative recordings of the sucrose data in Figure 4A.

1. The authors may wish to include a comment about whether bromide has the same effect on taste perception as chloride, and point out that gurmarin is a non-selective antagonist. Ideally, the nerve recordings should be done in T1r knockout mice to formally prove the mechanism. Although this may be beyond the scope of this work, a brief mention of this caveat seems warranted.

As described above, we added the nerve recording data using T1r3-KO mice and proved that the chloride-derived responses were attributed to T1rs.

We agree with the reviewers' pointing that a halide-specificity to T1rs is an interesting issue to be addressed in future studies.

1. Finally, the discussion would benefit from additional mention of ligand binding in relevant heterodimeric class C GPCRs, as well as the observation that chloride appears to work via a distinct mechanism despite its binding site being spatially very close to that of Gln.

The discussion regarding the chloride-dependent regulation of ligand-binding in other class C GPCRs as well as structurally related receptors (ANPRs) was described in the last paragraph of the Discussion. The relationship between the amino acid-binding and the chloride-binding was addressed in the third paragraph in the "Taste response to Cl– through T1rs in mouse" section in Results (p. 16, the next paragraph to the Figure 4 in the manuscript).

(This is a response to peer review conducted by Biophysics Colab on version 1 of this preprint.)

Endorsement statement (3 October 2022)

The preprint by Galles et al. reports the generation of pyrrolysine-based aminoacyl-tRNA synthetases capable of incorporating fluorinated phenylalanine non-canonical amino acids into proteins expressed in either bacteria or mammalian cells. For the most extensively characterized synthetases, fluorinated phenylalanine derivatives were successfully incorporated into GFP and two membrane proteins (CFTR and Nav1.5) at expression levels adequate for biochemical studies, suggesting that the approach could be combined with multiple different structural and biophysical techniques. The work provides a valuable tool that will enable the functional role of cation-pi interactions to be interrogated in both soluble and integral membrane proteins.

(This endorsement by Biophysics Colab refers to version 2 of this preprint, which has been revised in response to peer review of version 1.)

Authors' response (20 July 2022)

GENERAL ASSESSMENT

This is an interesting preprint wherein the authors report the generation of pyrrolysine-based aminoacyl-tRNA synthetases capable of incorporating fluorinated phenylalanine non-canonical amino acids (ncAA) into proteins expressed in either bacteria or mammalian cells. Synthetase evolution was directed using para-methyl tetrafluorophenylalanine as an ncAA. The authors use several screens and assays to characterize individual synthetases using superfolder GFP to measure protein expression using fluorescence and then identify the incorporated ncAA using mass spectrometry. For the two most extensively characterized synthetases, a wide array of fluorinated phenylalanine derivatives can be successfully incorporated. Contaminating incorporate of phenylalanine can be detected when attempting to incorporate several ncAAs in E. coli, but this bleed through incorporation of phenylalanine is not observed for expression in mammalian cells. In the case of monofluorinated phenylalanine for expression in mammalian cells, incorporation in place of phenylalanine is observed in other regions of GFP outside the site directed using the amber codon, making it challenging to incorporate the less heavily fluorinated ncAAs. Finally, the authors demonstrate that GFP and two membrane proteins (CFTR and Nav1.5) can be expressed at levels adequate for biochemical studies with one of the synthetases in the presence of a trifluoro phenylalanine ncAA, suggesting that the approach should be feasible for combining with many structural and biophysical approaches. Overall, this is an interesting study that generates several new synthetases that have utility for incorporation of fluorinated phenylalanine derivatives that can be used for expression in both prokaryotic and eukaryotic expression systems and that would likely be feasible for use for structural and other mechanistic biophysical studies.

RECOMMENDATIONS

Revisions essential for endorsement:

1) The results and methods sections could be improved throughout by taking the space to provide the reader with a clearer conceptualization of each step in the process implemented by the authors to evolve the synthetase to incorporate fluorinated phenylalanine derivatives. What was the starting synthetase (presumably from ref 39)? Which positions were subject to random mutagenesis? Is the library a new one or one used previously? Can the authors provide the sequences for the different evolved synthetases characterized here? In the methods it is stated that 17 unique sequences were identified, but why not report what they are? Might it be worthwhile discussing how the present results compare with earlier attempts to evolve the synthetase for other ncAAs? It was also not entirely clear to us how do the positive and negative selection screens work. How many rounds of positive-negative selection have been made? Which mutations have been identified in the variants? Why do the results shown in Fig. 2B seem to disagree with some of the results shown in Fig. 2C? C10 is mentioned in the methods section but not shown in Fig. 2C. More extensive citation of prior work would help but the work will be much more accessible to the general audience if the authors explain everything conceptually in the results section and add more details to the methods section. The screening protocol used to identify synthetase variants is explained in greater detail in the methods, however the corresponding Figure (Fig 2) is not very well explained, please provide more explanation in the legend or the text about the results presented. Round 1 and Round 2 correspond to 2 different rounds of positive-negative screening? Panel C: it's not clear what round 1 and round 2 stands for and why some of the mutants are in round 1 and why some others in round 2. Were the UP50 plots done for the" top performing synthetases" in both rounds? Please specify. Please state what the crosses mean in Fig. 2B.

We thank you for these comments.

-The specifics of the library and the active site sequences will be included in the final published version and were only omitted due to the nature of preprint publishing (to which we are still acclimating).

-In the results section we clarified what is meant by "rounds" of selection as simply two independent attempts at screening the same library with the same starting amino acid.

-Characterization of C10 was not included because although it came out of the screen as its own "hit," we realized its sequence was the same as one of the other enzymes identified.

-Our recent methods paper Galles et al (MIE, 2021) as cited is a recent and very extensive step-by-step guide from our group describing the screening method. This paper goes into detail on the positive and negative screening, and includes and informative cartoon figure.

-The positions with X's produced unreliable fluorescence data.

2) The authors demonstrate that they can incorporate different fluorinated phenylalanine residues into GFP and that under similar conditions two membrane proteins can be expressed at reasonable levels. What is less clear is how well the ncAAs will be incorporated into different membrane proteins. Might the procedures employed for GFP work less effectively for other proteins? The claim that the technique is widely applicable to membrane proteins would be strengthened if the authors could provide evidence for robust incorporation of ncAAs into membrane proteins, but even if this is too challenging for the time being, the authors should openly discuss problems that might be encountered or what makes them optimistic that the synthetases developed here will be effective at incorporating ncAAs into proteins beyond what they have shown for GFP.

We appreciate this point. In this respect, the western blots of CFTR and Nav 1.5 are intended to indicate relative expression compared to Wild Type; that being said, we and others have found that relative expression with synthetase is target- and position-dependent. In our opinion, the targets shown, two completely unrelated membrane proteins (CFTR and Nav 1.5) and GFP, cover a broad spectrum of potential uses. In the lab we have shown rescue in additional soluble and membrane proteins but those are related to specific future projects and beyond the scope of this study.

Note that the reviewer suggestion below (#3- functional characterization of the rescued Nav 1.5 channel) provides a route to provide further evidence on the utility of the system and the robustness of expression. We accomplished this and included it in the revised preprint (see below).

3) One opportunity for demonstrating robust trifluorophenylalanine incorporation into Nav1.5 might be to include functional data demonstrating that the gating properties of the channel are altered compared to control. Is the F1486 position sufficiently sensitive for a functional readout to provide at least qualitative information about the extent of ncAA incorporation? This would also demonstrate trafficking of the protein to the membrane as a functional channel. Although it is difficult to measure the intact molecular weight of hCFTR and hNaV 1.5 proteins due to their size by MS, have the authors tried LC-ESI-MS/MS analysis following enzymatic digestion? This could conceivably help to validate not only the incorporation of fluoro-Phe ncAAs, but also the site specificity of incorporation.

We appreciate and have now addressed these points. See new figure 7 with patch clamp evidence of macroscopic expression (7G through 7J) and MS/MS spectra for F1486(2,3,6F Phe) Nav 1.5 (7F). Note that we did not expect a large functional effect of incorporating tri-fluoro Phe into this position, so showing rescue via unbiased biochemical (western blot) indication of full length expression is preferred (Figure 7C-D. Unsurprisingly, encoding of 2,3,6 trifluoro Phe at F1586 was functionally tolerated; large (multi nano Ampere), normally activating and inactivating currents were observed. (Fig 7G). However, as shown in the revised paper, we did discover that incorporation subtly enhanced inactivation (left shift in steady state inactivation and impaired recovery from inactivation Fig 7 I-J). As the binding of the IFM inactivation motif to its inactivated state receptor in Na__v_ _is believed to be driven by hydrophobic sources, subtle enhancement of inactivation via fluorination is consistent with the idea that fluorination can, in some cases increase stability of hydrophobic cores. We expound upon this in the relevant section of the results.

Additional suggestions for the authors to consider:

1) The sfGFP protein samples purified for intact LC-ESI-MS analysis can be used for MS/MS analysis. Most mass spectrometers have MS/MS capability. The protein sequences and the structures of F-Phe ncAAs are known. All these make the MS/MS validation applicable. Most importantly, the results would provide strong evidence of site-specific encoding of F-Phe in proteins.

Thank you for this suggestion. To most efficiently address this point and above #3, we expressed and purified F1486(2,3,6F Phe) Nav 1.5 and subjected it to tryptic digestion and MS/MS. These data now comprise figure 7F. Indeed, these data confirmed incorporation at position F1486.

2) Although a soluble protein was used to test the synthetases, the presentation gives the impression that the ultimate goal is for use on membrane proteins. Although membrane proteins are of interest to many and to the authors, why not present it as useful for both soluble and membrane proteins? Are there any known example of cation-pi interactions mediated by Phe in soluble proteins that would be worth investigating? A more general point is the authors could provide better framing or context by discussing how important cation-pi interactions are in proteins and what we know about them. In that regard, the intro would benefit from a few more sentences giving examples of important cation-pi interactions, and/or summarizing briefly findings of the in silico studies that are mentioned.

This suggestion is reasonable; as noted, our group's focus on membrane proteins affects the framing and discussion. That said, we do believe that the system will have broad utility. We edited the introduction and discussion to better reflect this. We also recently published a review article that details a wide range of cation-pi examples in membrane proteins (cited in this paper- Infield et al. JMB, 2021). This paper also discusses soluble proteins and examples of soluble domains of membrane proteins that have cation-pi interactions.

3) Could the introduction of the ncAA affect GFP fluorescence? Along these same lines, could the author explain why they select residue N150 for the introduction of the ncAA?

Thank you for this comment. Previous work has shown that fluorinated aromatic analogs do not appreciably affect fluorescence of this GFP design. We have added the relevant citation (Miyake-Stoner et al, Biochemistry, 2010) to the paper. Position N150 was chosen because it is extremely popular in the field; it has been used for dozens of studies reporting new synthetases. This enables important context when evaluating new synthetases that have been discovered.

4) Providing the specific sequences of sfGFP-His expressed in E coli and HEKT cells, and adding the expected Dmass for N150F would help readers to better understand the intact ESI-MS data presented in the paper and it's also hard to read the labels in Fig.4.

We added these protein sequences as a new Supplemental figure (5). We also added text on page 10 to clarify that the substitution of asparagine with phenylalanine yields a mass change of +33 Da.

5) The author might consider citing Last et al. as it features and interesting role of Phe residues in anion selectivity in the Fluc channel (Last et al. (2017) eLife 6:e31259).

Thank you for pointing this out; we've now mentioned this interesting study / mechanism into the introduction of the paper.

6) Table 1, shows DG in the binding energy measurements but we don't recall seeing in the manuscript how DG was calculated. Also, we may be missing something, but the theoretical quantum calculations referenced in the text (ref 24) will give a result in DE as energy. We are also curious about the meaning of the PHE% (Table 1 as well). How was it calculated? What kind of information is it providing?

The calculations were described under the methods section "Quantum calculations of cation pi binding potential" (at the very end).

Phe% is a simple transformation of the data- the percentage of cation pi binding ability for a given species as compared to the native phe, which is the strongest interactor. We have added a sentence better explaining this is in the results section.

(This is a response to peer review conducted by Biophysics Colab on version 1 of this preprint.)

Consolidated peer review report (12 May 2022)

GENERAL ASSESSMENT

This is an interesting preprint wherein the authors report the generation of pyrrolysine-based aminoacyl-tRNA synthetases capable of incorporating fluorinated phenylalanine non-canonical amino acids (ncAA) into proteins expressed in either bacteria or mammalian cells. Synthetase evolution was directed using para-methyl tetrafluorophenylalanine as an ncAA.  The authors use several screens and assays to characterize individual synthetases using superfolder GFP to measure protein expression using fluorescence and then identify the incorporated ncAA using mass spectrometry. For the two most extensively characterized synthetases, a wide array of fluorinated phenylalanine derivatives can be successfully incorporated. Contaminating incorporate of phenylalanine can be detected when attempting to incorporate several ncAAs in E. coli, but this bleed through incorporation of phenylalanine is not observed for expression in mammalian cells. In the case of monofluorinated phenylalanine for expression in mammalian cells, incorporation in place of phenylalanine is observed in other regions of GFP outside the site directed using the amber codon, making it challenging to incorporate the less heavily fluorinated ncAAs. Finally, the authors demonstrate that GFP and two membrane proteins (CFTR and Nav1.5) can be expressed at levels adequate for biochemical studies with one of the synthetases in the presence of a trifluoro phenylalanine ncAA, suggesting that the approach should be feasible for combining with many structural and biophysical approaches. Overall, this is an interesting study that generates several new synthetases that have utility for incorporation of fluorinated phenylalanine derivatives that can be used for expression in both prokaryotic and eukaryotic expression systems and that would likely be feasible for use for structural and other mechanistic biophysical studies.  

RECOMMENDATIONS

Revisions essential for endorsement:

1) The results and methods sections could be improved throughout by taking the space to provide the reader with a clearer conceptualization of each step in the process implemented by the authors to evolve the synthetase to incorporate fluorinated phenylalanine derivatives. What was the starting synthetase (presumably from ref 39)? Which positions were subject to random mutagenesis? Is the library a new one or one used previously? Can the authors provide the sequences for the different evolved synthetases characterized here? In the methods it is stated that 17 unique sequences were identified, but why not report what they are? Might it be worthwhile discussing how the present results compare with earlier attempts to evolve the synthetase for other ncAAs? It was also not entirely clear to us how do the positive and negative selection screens work. How many rounds of positive-negative selection have been made? Which mutations have been identified in the variants? Why do the results shown in Fig. 2B seem to disagree with some of the results shown in Fig. 2C? C10 is mentioned in the methods section but not shown in Fig. 2C. More extensive citation of prior work would help but the work will be much more accessible to the general audience if the authors explain everything conceptually in the results section and add more details to the methods section. The screening protocol used to identify synthetase variants is explained in greater detail in the methods, however the corresponding Figure (Fig 2) is not very well explained, please provide more explanation in the legend or the text about the results presented. Round 1 and Round 2 correspond to 2 different rounds of positive-negative screening? Panel C: it’s not clear what round 1 and round 2 stands for and why some of the mutants are in round 1 and why some others in round 2. Were the UP50 plots done for the” top performing synthetases” in both rounds? Please specify. Please state what the crosses mean in Fig. 2B.

2) The authors demonstrate that they can incorporate different fluorinated phenylalanine residues into GFP and that under similar conditions two membrane proteins can be expressed at reasonable levels. What is less clear is how well the ncAAs will be incorporated into different membrane proteins. Might the procedures employed for GFP work less effectively for other proteins? The claim that the technique is widely applicable to membrane proteins would be strengthened if the authors could provide evidence for robust incorporation of ncAAs into membrane proteins, but even if this is too challenging for the time being, the authors should openly discuss problems that might be encountered or what makes them optimistic that the synthetases developed here will be effective at incorporating ncAAs into proteins beyond what they have shown for GFP.

3) One opportunity for demonstrating robust trifluorophenylalanine incorporation into Nav1.5 might be to include functional data demonstrating that the gating properties of the channel are altered compared to control. Is the F1486 position sufficiently sensitive for a functional readout to provide at least qualitative information about the extent of ncAA incorporation? This would also demonstrate trafficking of the protein to the membrane as a functional channel. Although it is difficult to measure the intact molecular weight of hCFTR and hNaV 1.5 proteins due to their size by MS, have the authors tried LC-ESI-MS/MS analysis following enzymatic digestion? This could conceivably help to validate not only the incorporation of fluoro-Phe ncAAs, but also the site specificity of incorporation. 

Additional suggestions for the authors to consider:

1) The sfGFP protein samples purified for intact LC-ESI-MS analysis can be used for MS/MS analysis. Most mass spectrometers have MS/MS capability. The protein sequences and the structures of F-Phe ncAAs are known. All these make the MS/MS validation applicable. Most importantly, the results would provide strong evidence of site-specific encoding of F-Phe in proteins.

2) Although a soluble protein was used to test the synthetases, the presentation gives the impression that the ultimate goal is for use on membrane proteins. Although membrane proteins are of interest to many and to the authors, why not present it as useful for both soluble and membrane proteins? Are there any known example of cation-pi interactions mediated by Phe in soluble proteins that would be worth investigating? A more general point is the authors could provide better framing or context by discussing how important cation-pi interactions are in proteins and what we know about them. In that regard, the intro would benefit from a few more sentences giving examples of important cation-pi interactions, and/or summarizing briefly findings of the in silico studies that are mentioned.

3) Could the introduction of the ncAA affect GFP fluorescence? Along these same lines, could the author explain why they select residue N150 for the introduction of the ncAA?

4) Providing the specific sequences of sfGFP-His expressed in E coli and HEKT cells, and adding the expected Dmass for N150F would help readers to better understand the intact ESI-MS data presented in the paper and it's also hard to read the labels in Fig.4.

5) The author might consider citing Last et al. as it features and interesting role of Phe residues in anion selectivity in the Fluc channel (Last et al. (2017) eLife 6:e31259).

6) Table 1, shows DG in the binding energy measurements but we don’t recall seeing in the manuscript how DG was calculated. Also, we may be missing something, but the theoretical quantum calculations referenced in the text (ref 24) will give a result in DE as energy. We are also curious about the meaning of the PHE% (Table 1 as well). How was it calculated? What kind of information is it providing? 

REVIEWING TEAM

Reviewed by:

Ana I. Fernández-Mariño, Research Fellow (K.J. Swartz lab, NINDS, USA): ion channel structure and mechanism, electrophysiology and molecular biophysics

Yan Li, Director Proteomics Core, NINDS, USA: protein mass spectrometry

Chloé Martens, Assistant Professor, Université Libre de Bruxelles: membrane protein structural biology, membrane transport

Kenton J. Swartz, Senior Investigator, NINDS, USA: ion channel structure and mechanisms, chemical biology and biophysics, electrophysiology and fluorescence spectroscopy

Curated by:

Kenton J. Swartz, Senior Investigator, NINDS, USA

(This consolidated report is a result of peer review conducted by Biophysics Colab on version 1 of this preprint. Minor corrections and presentational issues have been omitted for brevity.)

Consolidated peer review report (23 September 2022)

GENERAL ASSESSMENT

In this manuscript, Tiemann, J., et al. take on a large-scale exploration of how mutations associated with disease impact calculated stability and conservation scores across the entire membrane proteome. The aim was to gain mechanistic insight into the causes of pathogenicity of missense mutations of human membrane proteins and verify whether, as is the case for soluble proteins, mutational destabilisation of membrane proteins can explain disease. To do so, the authors use a framework they previously developed, using measures of stability change (ΔΔG) and sequence conservation (ΔΔE, the GEMME score) to predict fitness effects of mutations with large-scale mutational data (Høie et al., 2022).

By conducting a proteome-wide analysis of missense variants in human membrane proteins, the authors find decisively that pathogenic mutations are heavily enriched within the transmembrane region of membrane proteins. In addition, they report that they can sometimes use their calculated properties to classify residues based on their potential roles in stability or function, and that stability appears to be a major determinant of conservation and likely pathogenicity for GPCRs. 

The authors thus make meaningful strides towards explaining the clinical impact of variants within membrane proteins, a currently under-characterized yet important category of proteins. The analyses have been conducted in a rigorous way, and the data and protocols are openly available. This work will be of interest to researchers working on membrane proteins as well as those applying computational methods to biophysical systems.

On the other hand, the choices made by the authors in terms of presentation make the identification of the main conclusions of the paper challenging. In part, this is likely due to fundamental technical challenges associated with calculating biophysical properties for membrane proteins. In addition, although the analysis was performed at the scale of the proteome, due to the decision to only consider X-ray crystallography structures, the number of proteins analyzed is rather small (15). It thus remains unclear how the findings are transferable to other membrane proteins and how robust the comparison between the different functional classes is. 

RECOMMENDATIONS

Revisions essential for endorsement:

1.     The authors are careful with what they claim, to the point where it becomes difficult to interpret the major messages. It appears there are many contributing factors to noise within these assays, resulting in complex figures that make it hard to interpret the data. The goal of presenting the data without overinterpreting it is noble, and the difficulty of digesting and presenting the comparisons in this work should be emphasized, but the complexity of the results made it difficult for reviewers to interpret without more robust processing. Further, we were not always certain how each result fits into the overall argument, which from our reading is whether the performance of predictors for classifying pathogenic mutations based on conservation and stability calculations provides insight into the mechanisms underlying membrane protein disease. Overall, we feel that clarifying the unifying argument of the manuscript and simplifying the figures would greatly improve the comprehensibility of this work. This could be achieved with one of the following approaches, although we leave the final choice to the authors: 

• The manuscript could attempt to answer the following question: “Can existing methods be used to computationally determine whether pathogenic mutations are due to stability?” It would then explore why this question can or cannot be answered with the current analysis pipeline and existing tools. The answer is likely that the current tools are insufficient and the manuscript would thus point towards a future area of growth to be able to address the question.

• The manuscript could focus on presenting the dataset. The results would be presented as preliminary examples of the kind of information that can be extracted and the type of analysis that may be done. In this case, claims such as “stability causes x% of pathogenic mutations” should be avoided, and the most important aspect of the manuscript would be that it accompanies a well-curated and openly available dataset, and provides links to it. In that context, the authors should mention whether there are existing curated and/or established databases of (human) membrane proteins, and how the dataset of putative membrane proteins compares with these resources.

• The manuscript could focus on presenting the “computational approach”, which consists of mapping ddG-ddE, combined with an analysis of the localization of pathogenic (and non-pathogenic) mutations and the types of mutation (conservative, non-conservative etc.). Revisions would be needed to present results as examples of the kind of information this approach may provide.

• The manuscript could possibly make a clear and compelling case for the idea that mutations of membrane proteins cause disease either because they destabilize the protein or because they occur at sites that are directly involved in function. This would require major revisions of the results and a systematic, clear and robust combined analysis of quadrant-location, protein-region-location, and amino-acid-type substitution.

Related to the above, it would be useful to clarify in the introduction what is expected from the study upfront: did the authors expect that the picture that would emerge would indeed be the same for membrane proteins as for soluble proteins? Are there different degradation pathways for these two classes of proteins and is a loss of stability expected to have different consequences or not? In the end, the role of destabilization is rationalized in terms of buriedness and amount of physico-chemical change upon mutations. Hence, are the results of the study saying something about the mechanisms of disease variants or simply about the physico-chemical composition and topology of membrane proteins? To answer this point, we suggest contextualizing the study more by expanding on the published literature. This would also clarify that the membrane protein folding field is very far behind the soluble protein folding field, and, as a result, that we cannot expect the methods that work for soluble proteins to work for membrane proteins, or even if methods will mature to the point that they do yield predictive results for membrane proteins. 

2.     In general, uncertainties need to be better quantified and discussed and statistical tests included. For example:

• The low correlation of Rosetta estimates of ΔΔG and experimental ΔΔG is 0.47, which means less than 25% of ΔΔG is accounted for by Rosetta. This uncertainty needs to be considered more carefully: it will likely affect the AUC (i.e. is AUC(ΔΔG) < AUC(ΔΔE) because not all mutations are pathogenic due to stability, or is this a mere consequence of the uncertainty of ΔΔG estimates?) and the number of points in the different quadrants (how many of the points in a quadrant are false-positives or false-negatives, etc., and can we guess which they are by using other information such as the protein region, aa-type change, ΔΔE value, etc?). 

• A variant may fall in the “wrong” ΔΔG-ΔΔE quadrant because of the mentioned (large) ΔΔG error, but also because of ΔΔE errors. This needs to be considered. Some estimate of the ΔΔE error needs to be made (e.g. by bootstrapping the alignment). Even in an ideal case in which ΔΔE is dependent only on ΔΔG, i.e. that both ΔΔG_Rosetta and ΔΔE are estimates of a “true” ΔΔG, not all points would fall in a y = x line in the ddE-ddG plane. How many points would there be in each of the quadrants because of mere estimation errors?

• As the authors state, quadrant IV has few points. But it also seems that there are more blue points than red points in regions further away from the axes. Could the author comment on this observation? Is there a tendency for the ΔΔG measure to “over predict” pathogenicity ?

• Within the manuscript the authors widely compare different groupings to drive their narrative. For example, on line 115 the authors discuss the enrichment of pathogenic mutations within the transmembrane domains, which then leads to many subsequent explorations of why TMs may be involved in disease. For this comparison, there is a large and visible significant difference, thus there may not be a need for a statistical test for significance. However, there are many other comparisons that are harder to interpret due to multiple different groupings, complex data representation, and at its core a fundamentally complex study. In these cases, we would like to see more robust statistical tests. For example, on line 184, after breaking up data in 2B based on ΔΔG and ΔΔE cutoffs, the authors write “...only a few variants (14.2%) falling in the quadrant of low ΔΔE and ΔΔG…” – it is unclear what a few means or if this is a significant reduction in variants compared to other quadrants. 

3.     Regarding the performance of Rosetta to measure ΔΔGs:

• The authors state that pathogenic mutations causing loss of stability are more often located in the interior of the protein (buried), implying bigger physico-chemical property changes. Isn’t that expected from Rosetta design? Indeed, while the analysis of the distribution of variants among protein regions (buried, etc.) and mutation-type (hydrophobic-to-hydrophobic, etc.) does add additional information to support the hypothesis that in some cases stability loss causes disease, it is important to recognize that this is not completely independent evidence because any ΔΔG predictor should somehow capture the observed patterns. 

• ROC curves are used to determine how well ΔΔG guides pathogenicity, as a follow up to the observations that pathogenic mutations are enriched in TM regions of membrane proteins. The intuition here is that deleterious mutations within TMs are likely disrupting folding and therefore a ΔΔG-based predictor should do relatively well. However, the authors find that Rosetta-based ΔΔG calculations do not do well in all membrane proteins with benign-like and pathogenic mutations (Figure 2A) and solved crystal structures. In contrast, ΔΔG works quite well when trained solely on GPCRs (Figure 3A). The interpretation of this could be that stability is not a major driver of membrane protein disease – however, in many cases it is, such as Rhodopsin and CFTR. In contrast, another explanation is that Rosetta doesn’t predict stability well for mammalian membrane proteins, and in fact the authors discuss this at length in the limitations of the study section, explaining this is because Rosetta is trained on many bacterial beta barrel membrane proteins. We appreciated this section but would have preferred more of this discussion earlier on as it could aid in understanding why the ΔΔG predictors don’t perform accurately, as presented in Figure 2A. 

• Could the authors clarify what they mean by “where the Rosetta energy function suggested a potential incompatibility between the experimental structure and the Rosetta energy function”? 

4.     Regarding ΔΔE, in the present work, there is an implicit assumption that the constraints that operate during evolution of the aligned sequences, across species, as captured by GEMME, are the same constraints that affect the variants within a population, and therefore determine whether a variant will be pathological/non-pathological. This is a major assumption that needs to be spelled out and discussed. Mentioning this will help interpret “misplaced” points of the ΔΔE-ΔΔG map.

Additional suggestions for the authors to consider:

1.     The comparison of pathogenic/non-pathogenic mutations should consistently be made across the various sections of the paper. In too many cases in the present version of the paper this comparison is not emphasized. In some cases, the distribution of variants is described, without clearly differentiating pathogenic from non-pathogenic. In other cases, only pathogenic variants are considered, without comparing with the non-pathogenic cases.

2.     Moving the section on the two specific proteins to the end of results would likely improve the flow of the paper. The A/B x ΔΔE-ΔΔG plane analysis would be presented first, then the A/B x ΔΔE-ΔΔG x “protein regions” analysis, and finally the A/B x ΔΔE-ΔΔG x regions x “aa-type” analysis before ending with examples.

3.     The choice to restrict the analysis to X-ray crystallography structures from the PDB is not obviously well suited. Indeed, the coverage of membrane proteins by the PDB is rather low, and the authors found that less than 30% of all annotated human membrane proteins have at least some part resolved. One of the potential advantages of the AlphaFold database is to improve this coverage, and the analyses presented by the authors would thus benefit from considering predicted models displaying high confidence values.

4.     In Figure 2, the authors define two classes of variants in their dataset, group A (pathogenic variants) and group B (benign or non-pathogenic with an allele frequency > 9.9 · 10^-5). Then they tested their models’ ability to distinguish between groups A and B by constructing ROC curves for Rosetta ΔΔG and GEMME ΔΔE. To visualize variant effects and further classify variants, they plotted individual variants along a ΔΔG vs. ΔΔE plot. They then use this plot to further classify variants based on their combined ΔΔG and ΔΔE values. The allele frequency cutoff is so important for generating group B that all downstream analysis is dependent on this. But because these residues are coming from a much more limited set of proteins, we think it would be useful to include a comparison showing that the gnomad allele frequency > 9.9 x 10^-5 cutoff remains informative for differentiating between benign and pathogenic residues.

5.     In Figure 3, the authors apply their analysis to variants across all GPCRs, as well as just GPCR transmembrane regions. The AUC curves in panel A are much more accurate when applied to just this protein family, as also seen in panel B where variants fall into very clear subpopulations within each quadrant. The illustration and category definitions on the left of panel C are a helpful guide for the discussion of different variant types and their relevance to stability of the protein versus function in a unique way, however the plot on the right of panels C and D is confusing and not immediately intuitive making it difficult to consider comparisons that are discussed within the text. Indeed, the authors state that “Pathogenic variants in GPCRs, especially in the transmembrane region, lose function mostly by loss of stability”. Comparing these two panels, it is concluded that the pathogenic variants that do not lose stability are more often found in the TM regions of GPCRs compared to all datasets. This is somewhat confusing and the numbers supporting this affirmation in Fig 3C seem quite low.

6.     The authors do not extensively discuss their results in the context of the membrane protein field nor the specific membrane proteins they highlight such as Rhodopsin and GTR1 (Figure 4). For Rhodopsin, at least, there has been extensive work done on its folding by Johnathan Schlebach’s lab and others, including a mutational scan. It could be useful to at least contextualize and contrast results here with previously published work. 

7.     In Figure 5, the authors consider whether the identities of the starting and mutant residues correlate with their overall quadrants. Panel A is extremely difficult to interpret. We are  also unsure how robust any differences are likely to be, given the uneven sampling and the small number of samples in some of the boxes. Narrowing the comparisons (changed vs. unchanged property, A vs B) would likely improve comprehension and may be more meaningful. Panel B is, on the other hand, a wonderful example of how to clearly display complex, multidimensional data in a comprehensible way. The well-demonstrated association of hydrophobicity and transmembrane stability is beautifully demonstrated directly from the data, and the potential discordance with evolutionary conservation as well. We find this correlation even more striking given that the hydrophobicity scale used here was explicitly determined in the context of transmembrane regions, but the variants are drawn from all regions of the targets. We were curious to know what percentage of these are drawn from the transmembrane vs. soluble regions of the targets.

REVIEWING TEAM

Reviewed by:

Willow Coyote-Maestas Paper Discussion Group, UCSF, USA: membrane proteins; high throughput experimental variant screening; developing assays for measuring how mutations break membrane proteins in order to explore how mutations alter folding, trafficking, and function of membrane proteins (see Appendix for group members).

Julian Echave, Professor, Universidad Nacional de San Martín, Argentina: theoretical and computational study of biophysical aspects of protein evolution.

Elodie Laine, Associate Professor, Sorbonne Université, France: development of methods for predicting the effects of missense mutations using evolutionary information extracted from protein sequences and/or structural information coming from molecular dynamics simulations.

Curated by:

Lucie Delemotte, KTH Royal Institute of Technology, Sweden

APPENDIX

Willow Coyote-Maestas Paper Discussion Group:

Feedback was generated in a meeting of the journal club involving:

Willow Coyote-Maestas

Christian Macdonald

Donovan Trinidad

Patrick Rockefeller Grimes

Matthew Howard

Arthur Melo

(This consolidated report is a result of peer review conducted by Biophysics Colab on version 1 of this preprint. Minor corrections and presentational issues have been omitted for brevity.)

Consolidated peer review report (9 September 2022)

GENERAL ASSESSMENT

This interesting preprint by Suárez-Delgado et al. explores the mechanism by which activation of the Hv1 voltage-activated proton channel is dependent upon both the voltage and pH difference across the membrane. The authors are the first to incorporate the fluorescent unnatural amino acid, Anap, into the extracellular regions of the S4 helix of human Hv1 to monitor transitions of S4 upon changes in voltage or pH. The authors first checked that Anap is pH insensitive for practical use in Hv1, where changes in local pH are known to occur when the voltage sensor activates and the proton pore opens. Anap was incorporated at positions throughout the S3-S4 linker and the extracellular end of S4 (up to the 202nd residue) of hHv1 and some positions showed clear voltage-dependent changes in fluorescence intensity. The authors also obtained fluorescence spectra at different voltages and observed no spectral shifts, raising the possibility that voltage dependent changes in fluorescence intensity could primarily be due to fluorescence quenching. Upon mutation of F150, the Anap signal at the resting membrane voltage increased, suggesting dequenching upon removal of F150. The authors also discovered that the kinetics of Anap fluorescence upon membrane repolarization have two phases (rapid and slow) under certain pH conditions and that there is a pH- dependent negative shift of the conductance-voltage (G-V) relation compared with the fluorescence-voltage (F-V) relation in some mutants. The biphasic kinetics of the fluorescence decay upon repolarization were explained by modelling a slower transition of return from intermediate resting state to a resting state. The pH-dependent shift of the G-V relation from the F-V relation provides insight into mechanisms of ΔpH-dependent gating of Hv1, a longstanding enigma. Overall, the approaches are rigorous, the figures show important results, and this work paves the way for the use of Anap fluorescence to study Hv1 gating and modulation.

RECOMMENDATIONS

Revisions essential for endorsement:

1) In its current form, the narrative of the preprint has two threads. One on the mechanisms of Anap fluorescence changes (mainly quenching) and another on a previously unappreciated transition of the voltage sensor, as revealed by Anap. Our impression is that the preprint suffers somewhat from this split focus, which could be resolved by explaining why Anap was used to explore voltage sensor activation in Hv1 in the introduction. Perhaps the authors could also explain the advantage of smaller sized fluorophores compared to other maleimide-based fluorophores earlier in the introduction, or the utility of being able to insert Anap into transmembrane segments. The authors should more clearly point out how they exploited the advantages of Anap as a tool in this study. It would furthermore be helpful to discuss previous studies using nongenetic tools for VCF and spell out how they have delineated key aspects of Hv1, which would help to emphasize how several positions studied here (for example, 201 and 202) could not be labelled with cysteine-based fluorophores.

2) We think the authors should be cautious about understanding the physicochemical nature of Anap using prodan as a model. It would be helpful to discuss the possibility that undetected spectral shifts due to a nonquenching mechanism could be overlooked, even though major signal changes can be explained by fluorescence quenching in their data. Regarding the mechanisms of remaining voltage-dependent fluorescence changes of F150A-A197Anap, it would be helpful for the authors to suggest possible ideas about which residues might account for remaining signals.

The beautiful spectral data for Anap is impressive. However, the physicochemical basis of the fluorescence change of Anap cannot be understood by simple extension of findings for prodan, which shows structural similarity to Anap. Our understanding is that changes in Anap fluorescence can only reveal a change in the structural relationship between Anap and one of its neighbors because the physicochemical basis of Anap fluorescence is complicated. For example, fluorescence could also be affected by the electrostatic environment, stretch of peptide bond, etc. Previous studies, including those of TRP channels, showed that the kind of environmental changes that Anap faces in ion channels do not necessarily induce large spectral shifts, unlike in cell-free spectral analyses using distinct solvents. Further, only minor shifts in spectra occur upon local structural change, as seen in previous work including Xu et al. Nat. Commun. 2020 11:3790. Such minor shifts could be perhaps overlooked even when Anap is incorporated into S4 and exposed to environmental change. Therefore, it is not easy to decode the physicochemical basis of Anap fluorescence changes. F150A-A197Anap has increased fluorescence and no change in spectral pattern, leading the authors to conclude that F150 quenches Anap fluorescence of A197 position. However, a significant amount of fluorescence change still occurs upon changes in membrane potential after F150 is changed to alanine (Figure 4). It is very likely that quenching is not the only mechanism underlying the observed voltage induced change of Anap fluorescence of Hv1. The authors suggest that remaining voltage-dependent fluorescence change of F150A-A197Anap could be due to interaction with other aromatic residues, but this has not been tested.

3) The current version of the preprint is missing important control experiments, ideally performed using western blots to measure protein expression or, if that is not possible, proton current and fluorescence measurements, to demonstrate that protein expression or functional channels are not seen for all mutants in the absence of ANAP (but in the presence of the tRNA and Rs construct).  A similar control for imaging would be to use ANAP alone without encoding. 

4) Aromatics in the S4 segment were ruled out as potential quenchers on the assumption that they would move together with Anap during gating. It should be noted, however, that Hv1 is a dimer and therefore a fluorophore attached to S4 in one subunit could be quenched by S4 aromatics in the neighboring subunit if were close to the dimer interface. In Fujiwara et al. J. Gen. Physiol. 2014 143:377-386, for example, W207 does not appear very far from labeled positions in the adjacent S4. This possibility should be mentioned in the discussion.

5) It is not clear whether the Anap spectra purely represent Hv1 incorporated into the plasma membrane or perhaps include signals from the cytoplasm or channels in internal membranes (whether assembled or incompletely assembled). It would be helpful to provide a more complete presentation of the data obtained and to provide more information in the Methods Section. In the Methods section, it is stated “The spectra of both fluorophores (Anap and mCherry) were recorded by measuring line scans of the spectral image of the cell membrane, and the background fluorescence from a region of the image without cells was subtracted”. How are signals from cell membranes specified in this method being discriminated from those associated with the cytoplasm and intracellular membranes? If spectral data include signals from free Anap in the cytoplasm or Hv1 in intracellular membranes, spectral shifts upon membrane potential changes will be difficult to detect, even when Anap is incorporated into Hv1 and senses environmental change by voltage-induced conformational change. In Figure 3E, wavelength spectra were shown as standardized signals for different voltages. Amplitude change would be demonstrated (spectrum at different voltages without standardization would be shown). In Figure 4, spectra were compared between A197Anap and F150A-A197Anap, showing increases of fluorescence in F150A-A197Anap. Was this signal measured at resting membrane potential? How does the spectrum change when the membrane potential is changed?

Rationales for the confirmation of signals originating from the cell surface for Hv1 Anap might include the observations that: a) some mutants showed slightly different spectral patterns (in particular, Q191Anap showed a small hump at longer wavelengths, which is proposed to represent FRET between mCherry and Anap) and b) signal intensity was voltage dependent (if signals originate  from endomembranes, they should not be voltage dependent). Mentioning these two points earlier in the text might help to alleviate concerns about the location of the protein that contributes to the measured signals.

6) In Fig 5, the fluorescence kinetics do not really match the current activation kinetics for panels A, B, and C.  Is there an explanation for this mismatch?  It would be helpful to have the fitted data in the figure. A more thorough comparison of the kinetics of currents and fluorescence would be helpful throughout the study. 

7) Which construct of hHv1 was used to obtain the data in Figure 6? Unless we missed it, this information is not provided in the text or figure legend. Is it for L201Anap? This figure also shows an intriguing finding that the G-V relationship is negatively shifted from the F-V relationship at pHo7-pHi7 but not at pHo5.5-pHi5.5. A shifted G-V relation with the same ΔpH contrasts with what has been reported in other papers. However, the authors did not really discuss this surprising finding in the light of previous references. Could the shift of the G-V relation between two pH conditions with the same ΔpH be due to any position-specific effect of Anap? If Figure 6 represents L201Anap mutant, the presence of Anap at L201 probably makes such shift of G-V curve in Figure 6C? The authors should openly discuss this finding in relation to what has been reported in the literature.

8) The authors suggest that the small hump near 600 nm in Figure 1E represents FRET between Anap and mCherry. It is surprising that FRET can take place across the membrane. Can the authors point to another case of FRET taking place across a cell membrane? One possibility might be that misfolded proteins place mCherry and Anap close to each other. It is also curious that only A191Anap did not show such a FRET-like signal. Also, if there is FRET, why wouldn’t this also contribute to the voltage-dependent changes in fluorescence?

9) F150A-A197Anap shows a leftward shift of the F-V relation compared with the G-V relation only when ΔpH=1. Another unusual finding with F150A-A197Anap is the very small shift of the G-V relation between ΔpH=0 and ΔpH=1, when other reports in the literature suggest it should be 40 mV or more. Are these peculiar properties simply due to the absence of Phe at position 150, which might play a critical role in gating as one of the hydrophobic plugs of Hv1?  To address this possibility, it would be ideal to compare different ΔpH values with and without F150 when Anap is incorporated at a different position (such as L201Anap). Regardless, it would be helpful to discuss this point.

10) In Figure 1E, I202Anap exhibits a blue shift in its spectrum suggesting the environment of Anap on I202 is more hydrophobic than the other sites. We presume these spectra were obtained at a negative membrane voltage, but the text or legend should clearly state how these were obtained. The authors should also explain whether the whole cell or edge was imaged. If these are at negative membrane voltages, might the Anap spectrum shift to higher wavelengths (i.e. more hydrophilic) when the membrane is depolarized? Did the authors find any spectral shift for I202Anap when doing a similar test as depicted in Figure 3E?

11) In Figure 3E, spectra are shown as normalized signals for different voltages, but an amplitude change should also be demonstrated by providing raw spectra at different voltages.

12) In Figure 4, spectra are compared between A197Anap and F150A-A197Anap, showing increase of fluorescence in F150A-A197Anap. Were these obtained at a negative membrane voltage? How do these spectra change when membrane potential is changed?

Additional suggestions for the authors to consider:

1) The authors propose that Anap fluorescence tracks an S4 movement involved in the opening of the channel. They also argue that the existence of more than one open state could explain why the increase in florescence upon depolarization lags the proton current in most cases. While they convincingly show that Anap is not pH sensitive per se, when incorporated into the protein, the fluorescence efficiency of the fluorophore could still be affected by protonation of channel residues in the immediate environment when the channel opens, even after S4 has completed its movement. To address this alternative explanation, the authors could use Hv1 mutants with strongly reduced proton conductance. Channels bearing mutations corresponding to N214R or D112N were used successfully to isolate Hv1 gating currents from the much larger proton currents (De La Rosa & Ramsey, Biophys. J. 2018 114:2844-2854; Carmona et al. PNAS 2018 115:9240-9245; Carmona et al. PNAS 2021 118: e2025556118). Perhaps, they could be used with patch clamp fluorometry as well?

2) The data showing that Hv1-197Anap is quenched by Phe at position 150 are very nice. Yet, it would be useful to show that the quenching is specific to F150 using a negative control. F149, for instance, is just next to F150 but points in a different direction, so its mutation to alanine should not affect Hv1-197Anap fluorescence.

3) A major finding of this work is the identification of a slow kinetic component that is highly sensitive to ΔpH. Earlier studies found that the ability of Hv1 to sense ΔpH is altered by some channel modifications, e.g., in the loop between TMH2 and TMH3 (Cherny et al. J. Gen. Physiol. 2018 150:851-862). Did the authors check whether any of these modifications alter the transition responsible for the slow kinetic component? For instance, a suppression of the transition resulting from a H168X mutation would help tighten the link to ΔpH sensing.

4) We understand that it is difficult to tightly control intracellular and extracellular pH when Hv1 is heterologously expressed in mammalian cells. The G-V relation is not always reliable because accumulation of protons or depletion of protons upon Hv channel activity will alter gating, as the authors have previously published (De La Rosa et al., J. Gen. Physiol. 2016 147:127-136). Could the kinetic analysis of Anap fluorescence be affected by similar alterations to proton concentration in the vicinity of Hv1? It would be helpful for the authors to comment on this specifically.

5) Quenching of Anap by Phe could be verified in cell free conditions using a spectrophotometer with different concentrations of Phe, or citing the literature if it has already been reported.

6) The authors did not cite any example of Anap incorporation into S4 helices, but there are several recent papers where Anap was utilized to probe motion of S4 in other channels. Examples include Dai et al., Nat. Commun. 2021 12:2802 and Mizutani et al. PNAS 2022 119:e2200364119.

7) In the Anap-free negative control (with only A197TAG plasmid transfection), the mCherry signal seems positive (Supplementary Figure 1, left row, second from the top). Is this due to unexpected skipping of the TAG codon to make mCherry-containing partial polypeptides? It would seem like an explanation is needed.

8) The data of Figure 3E are shown as data with different membrane voltages. But there is no information about membrane voltage for Fig. 1E and Fig. 2A and Fig. 4B. Are these from unpatched cells? Please clarify.

9) G-V relations are shown for F150A-A197Anap, but current traces of F150A-A197Anap are missing.

10) On Page 11, Line 303 says “experimental F-V relationship is positively shifted by 10 mV with respect to the G-V curve”. But looking at the data Fig5D, the shift at ΔpH=2 seems the opposite. Perhaps “positively” should be “negatively” in this sentence?

REVIEWING TEAM

Reviewed by:

Yasushi Okamura, Professor, Osaka University, Japan: voltage-sensing proteins, electrophysiology and fluorescence spectroscopy

Francesco Tombola, Associate Professor, University of California, Irvine, USA: ion channel mechanisms, electrophysiology and fluorescence spectroscopy

Christopher A. Ahern, Professor, University of Iowa, USA: ion channel mechanisms, non-canonical amino acidic mutagenesis

Curated by:

Kenton J. Swartz, Senior Investigator, NINDS, NIH USA

(This consolidated report is a result of peer review conducted by Biophysics Colab on version 1 of this preprint. Minor corrections and presentational issues have been omitted for brevity.)

Consolidated peer review report (22 June 2022)

GENERAL ASSESSMENT

GadC is a LeuT-fold antiporter that contributes to the survival of pathogenic bacteria under extreme acid stress by exchanging extracellular glutamate for intracellular GABA. The current study by del Alamo et al. uses DEER spectroscopy, in combination with AlphaFold2 (AF2), to investigate the conformational dynamics of GadC invoked by pH and substrates. AlphaFold2 was used to generate structural models, which likely represent different steps within the antiport conformational cycle of GadC, and use them to identify reporter residue pairs that undergo large inter-residue distance changes between the different conformations. By labeling these residue pairs with spin labels, the authors were able to use DEER spectroscopy to measure the distributions of inter-residue distances in the transporter under different conditions, namely high and low pH and the presence or absence of glutamate or GABA. They found many differences between high and low pH, but few differences triggered by the presence of substrates. They conclude that: (i) low pH triggers release of the intracellular C-terminal plug, unlocking the transporter and populating multiple conformational states; (ii) the bundle helices (TMs 1,2,6,7) do not behave as a rigid body; (iii) Alternating access in GadC does not involve large-scale movements of the intracellular and extracellular loops IL1 and EC4, as is believed to occur in other LeuT-fold transporters – instead, an extracellular “thin gate” in TM10 may be involved in permeation and substrate discrimination. They arrive at a model in which the substrates primarily affect the kinetics of conformational changes rather than the conformational equilibrium. This work also demonstrates the value of using AlphaFold2 to generate plausible structures tied to functional protein states to facilitate experimental design and data interpretation.

Overall, the work is very interesting and provides significant new insights into the transport mechanism of GadC.  The manuscript is clearly written, well organized, and the conclusions are reasonable. The DEER and CW EPR data are of high quality and the analysis of the experimental data is appropriate.  We have several recommendations that we feel would improve the presentation and interpretation of the experiments.

RECOMMENDATIONS

Revisions essential for endorsement:

1)    The authors assert that distance changes observed by DEER correlate well with in silico predictions of distance changes between the inward-open crystal structure and the putatively outward-open model generated by AF2 (c.f. Figure S15).  However, in many cases, the peak in the distribution assigned to a particular state does not correspond to the major peak, and sometimes corresponds to a low amplitude broad peak (maybe not surprising for a cycling transporter).  This raises the issue of whether interpretation of the experimental results could be biased by computational predictions. The authors should acknowledge the difficulty inferring functional states from DEER distributions and be very clear about which distances in the calculated distributions are being interpreted as functional states. Also, the site pairs that deviate from the trend in Fig. S15, such as 87/155 and 117/181, should also be included in the figure for transparency, even if the discrepancies are justified in the text.

2)    It would be important to report the distances, widths, amplitudes, and number of Gaussians used to fit each DEER trace.

3)    The authors should describe in the methods section how they determine transport rates. They mentioned that they use a Michaelis-Menten kinetic model, but they should then also describe how they use their data to calculate the initial rates for MM kinetics.

4)    The descriptions of the transport assay data in several of the figure legends are missing important experimental details: which substrate was incorporated in the liposomes, external pH of the liposomes, concentration of substrate. (Different details are missing in different figure legends.)

Additional suggestions for the authors to consider:

1)    Do the authors know whether the GadC protein has a preferred orientation in liposomes? It seems surprising that they see very little transport unless they have high external pH. Given the low internal pH (pH 5.5) and with a 50%-50% random orientation of proteins, one might expect inside-in transporters to be active.

2)    The authors should show an example of a size exclusion chromatography trace to support their statement that they can separate empty nanodiscs from protein-containing nanodiscs. This seems surprising considering the size and shape of GadC – perhaps they instead separate nanodiscs from free protein?

3)    What are the criteria used for choosing the amino acids to substitute the intrinsic Cys?

4)    Because nanodiscs are known to be unstable at acidic pH, could it be that the observed changes at low pH are partially due to pH-dependent changes of the nanodiscs?

5)    Page 4 mentions that no experimental evidence indicates formation of a quaternary assembly (dimer) in the lipid nanodiscs. Is this based on DEER measurements or other data? The authors should consider supporting their statement with data.

6)    How similar are the predicted distributions for different AF2 models in the same presumed functional state? Was there a reason for choosing just one?  Is there some way of combining distributions of all the models in a given functional state?

7)    The authors assert that the AF2 models more accurately fit the DEER data than the Rosetta models. What is the basis for this claim? Is there a way to add a supplemental figure showing a comparison of the distributions of each model relative to the DEER data in the same graph (maybe at just low pH)?

8)    The pH-driven association/dissociation of the C-terminus of GadC shown here is reminiscent of the well-studied “N-type” inactivation of voltage-gated potassium channels. Indeed, the authors even use the term “inactivation” here to describe the lack of transport at alkaline pH. A brief discussion of the similarity to K+-channel inactivation might be interesting to many readers.

9)    A brief description of the method used to model spin labels onto structural models to predict DEER distance distributions would be helpful.

10)  The authors may want to clarify what they mean by a “thin gate”.

REVIEWING TEAM

Reviewed by:

Eric G. Evans, Postdoctoral Researcher, University of Washington, USA: EPR, DEER, Rosetta

Rachelle Gaudet, Professor, Harvard University, USA: structure and mechanisms of LeuT-fold transporters

Yun Huang, Postdoctoral researcher, Weill Cornell Medical College: structural and dynamic mechanism of glutamate transporters

William N. Zagotta, Professor, University of Washington, USA: membrane protein dynamics

Curated by:

William N. Zagotta, Professor, University of Washington, USA

(This consolidated report is a result of peer review conducted by Biophysics Colab on version 1 of this preprint. Minor corrections and presentational issues have been omitted for brevity.)

Consolidated peer review report (8 September 2022)

GENERAL ASSESSMENT

The rationale behind the study:

While the activation mechanisms of Class A and Class B GPCRs have been extensively studied, little emphasis has been placed on the study of the dynamics of class F receptors such as Smoothened (SMO). Hence it is still elusive which motifs may take part in the transition from inactive to active conformations. Understanding the underpinnings of receptor activation in terms of residue networks, and their modulation by allosteric modulators, could help rational drug design, such as for novel SMO antagonists for cancer treatment.

Key findings and major conclusions:

Bansal, Dutta and Shukla perform extensive molecular dynamics (MD)  simulations in conjunction with Markov State Model theory for a range of conformational starting points (apo, agonist, and antagonist bound states) to elucidate a dynamic overview of SMO activation. This has mostly remained elusive despite the availability of inactive and active-state SMO structures. They reveal conserved motifs important for activation of class F receptors, which are distinct from other known activation motifs, including from class A or B GPCRs. The long-range MD simulations together with free energy calculations also identified three additional intermediate states between inactive and fully active SMO. Furthermore, they provide structural support for how the specific function of antagonists and agonists modulate the cholesterol tunnel and thereby modulate SMO’s activity. Finally, the authors present the dynamic allosteric pathway at atomistic resolution between the extracellular and intracellular side during activation and upon ligand modulation. Taken together, the authors provide a more detailed understanding of Class F GPCRs that could serve as the foundation for specific experimental validation studies.

The perceived strengths and weaknesses: 

The new perspectives on the conformational changes during activation of SMO are based on well-described MD simulations. The Class F activation mechanism is not well understood; hence the authors’ conclusions advance the field by identifying states that are distinct from class A GPCRs and how cholesterol can modulate SMO’s activity, resulting in a map of allosteric pathways for this receptor type. However, the stated uniqueness or proposed Class F-specific observations would be more definitive with additional analyses.

RECOMMENDATIONS

Revisions essential for endorsement:

1. The title seems too comprehensive for the present study. Please consider a title that more accurately summarizes the specific work in this manuscript.

2. [Methods - Pre-Production MD, page 20]: The authors chose a more complex membrane composition to mimic physiological cerebellar membranes that requires additional attention during equilibration. If this has not been undertaken (no note in the method section), we do recommend carefully investigating the lipid distributions/clustering, including unusual curvature, that might influence the receptors behaviour throughout the simulations, in particular if modulations by ligands are interpreted.

3. [Methods]: The authors should discuss convergence of the simulated clusters and energy landscape prior to conducting Markov State Modeling.

4. DRY motif:

   • Please clarify the statements about generalisation in Class F in light of the missing outward kinking. As this proline is present in other Class F receptors, it suggests that this activation feature is likely unique to SMO. Also this molecular switch should be compared to e.g. Rhodopsin, which also signals through Gi (see e.g. Hofmann et al. doi: 10.1016/j.tibs.2009.07.005).

   • The authors should consider additional evidence or be more careful in their statement that the conserved motif (W3.50-G5.39-M6.30) acts as a microswitch in SMO signal transduction. The authors claimed that it is analogous to the DRY motif in class A GPCRs. However, the DRY motif has been shown to be involved in both inactive and active states, validated by experimental data. The R3.50 in DRY motif forms an ionic lock in the inactive state and this ionic interaction is broken during receptor activation. It is unclear what interactions are formed between the W-G-M motif in SMO.

   • Similar to W-G-M, the D-R-E motif has also been claimed as an important site for signal transduction. We recommend caution in this conclusion. The authors mentioned there is an H-bond interaction between D473 and E518. Is there a water molecule between these two residues? The two residues have very low pKa for the carboxylate group and probably are devoid of hydrogens in physiological conditions. Figure 2C should include the R400.

5. The statement “SAG acts as an agonist by allosterically expanding the tunnel at the cholesterol interaction site” (line 252) may be incorrect according to at least two lines of evidence: 1) elongation of the 4-aminomethyl group of SAG converts it to an antagonist; 2) SMO variants containing mutations at the cholesterol binding site don’t respond to SAG as described in Deshpande et al (Nature 571, 284–288 (2019)). The agonist activity of SAG is most likely due to blocking cholesterol in the 7-TMs. The authors may want to change the statement and conclusion or provide strong evidence to support it.

Additional suggestions for the authors to consider:

1. [Fig S.19]: Validity of the MSM on 5 macrostates via the Chapman-Kolmogorov test: the predictions and estimates look identical. Please add a 95% confidence interval and provide scripts used for the calculation and plotting.

2. Did the authors try to simulate SMO with cholesterol bound to the cysteine rich domain (CRD)? The reorientation of CRD revealed by xSMO crystal structures is controversial in the field because this movement may be a result of crystal packing. It will be very interesting to test whether CRD can undergo this reorientation after cholesterol binding by MD simulation.

3. [Methods, page 19 line 332]: It is not entirely clear what preparation was done to the SANT1-SMO structure. Please rephrase the sentences to ensure reproducibility

4. [Methods]: General structure preparation: Where the structures solvated prior insertion into the membrane to avoid collapsing of cavities?

5. [Methods - MD, page 20]: The authors do not mention the used force-field. Please add.

6. [Figure S6]: For clarification and comparison (in context of uniqueness), please show the changes in the residues involved in the microswitch for b2AR (6.30, 5.58, 5.66 - also shown for Rhodopsin and others).

7. [Figure 3]: the authors compared the CRD-TMD junction between inactive and active states. How is the conformation of these residues compared to the determined structures of SMO?

8. [Results]: It is very interesting that three intermediate states have been determined between inactive and active states. It is unclear how these states (I1., I2, I3) are defined, besides the energy barrier. Are there any signature residues or motifs that can represent each intermediate state?

9. Cholesterol interactions, distributions and modulations could give valuable insight into their influence on the activation mechanism. As cholesterol is present in the simulations, this data could be easily screened for cholesterol-receptor interactions throughout the activation pathway.

10. Experimental structures have already revealed the conformational changes between inactive and active SMO, in particular, the shift of TM6 and the movement of W535. This should be clarified in the text and interpreted in light of the new results.

11. While the authors calculated the mean first passage times during the apo simulation, they did not correlate this to the presence and absence of agonists. This could give further insight into how those modulators are influencing the activation pathway.

12. [Methods]: The used analysis scripts could be deposited/made available (e.g. how the Chapman-Kolmogorov test was implemented).

13. The study would have a greater influence on the field by further investigations on the agreement between simulations and experiments.

REVIEWING TEAM

Reviewed by:

Tao Che, Assistant Professor, Washington University in St. Louis, USA: atomic-level understanding of the activation mechanisms of pain-related GPCRs

Xiaofeng Qi, Postdoctoral Researcher, UT Southwestern Medical Center, USA: structural biology of SMO receptors and Hh/Wnt signaling

Johanna Tiemann, Postdoctoral Researcher, University of Copenhagen, Denmark: MD simulations of activation mechanisms in Class A GPCRs

Curated by:

Alexander S. Hauser, Associate Professor, University of Copenhagen, Denmark

(This consolidated report is a result of peer review conducted by Biophysics Colab on version 1 of this preprint. Minor corrections and presentational issues have been omitted for brevity.)

Consolidated peer review report (26 August 2022)

GENERAL ASSESSMENT

Piezo1 and Piezo2 are stretch-gated ion channels that are critically important in a wide range of physiological processes, including vascular development, touch sensation and wound repair.  These remarkably large molecules span the plasma membrane almost 40 times.  Cryo-EM and reconstitution experiments have shown that Piezos adopt a cup-like structure and, by doing so, curve the local membrane in which they are embedded.  Importantly, membrane tension is a key mediator of Piezo function and gating, an idea well-supported several independent studies. Cells have varied three-dimensional shapes and are dynamic assemblies surrounded by plasma membranes with complex topologies and biochemical landscapes.  How these microenvironments influence mechanosensation and Piezo function are unknown.

The current preprint by Zheng Shi and colleagues asks how the shape of the membrane influences Piezo location.  The authors use creative approach involving methods to distort the plasma membrane by generating “blebs” and artificial “filopodia”.  Overall, the work convincingly shows that the curvature of the lipid environment influences Piezo localization.  Specifically, they show that Piezo1 molecules are excluded from filopodia and other highly curved membranes. These experiments are well controlled and the results fully consistent with previous structural and biochemical work.  Furthermore, the work explores the hypothesis that a chemical modulator of Piezo1 channels called Yoda1 functions by “flattening” the channels, a movement previously proposed to be linked to mechanical gating.  Consistent with this model, the authors show that Yoda1 application is sufficient to allow Piezo1 channels to enter filopodia. While the flattening model is provocative hypothesis, hard evidence awaits structural verification.

Overall, the preprint by Shi and colleagues will be of interest to scientists studying how mechanical forces are detected at the molecular level.  The work introduces important concepts regarding how the shape of cellular membranes affects the movement and function of proteins within it. The technical advance for changing the shape of a plasma membrane is of note. 

RECOMMENDATIONS

Revisions essential for endorsement:

As is evident from the comments below, our endorsement of the study is not dependent on additional experiments.  However, we feel more experimental clarification is needed, that providing clearer images would be helpful, and, most importantly, we would like alternative conclusions and caveats to be mentioned.

1. Can the authors comment on the link between the conclusions that (1) the presence of filopodia prohibits Piezo1 localization (Fig 1) and (2) Piezo1 expression prohibits the formation of filopodia (Fig 3). As it stands, it is hard to understand if there is a cause and effect relationship here or if these are separate, unrelated observations? We recommend revising the discussion to clarify.

2. When comparing the images of Fig. 2A, B to those of Fig. 2C, D, it appears that bleb formation induces a drastic enrichment of Piezo1 in the bleb membrane. Is this due to low membrane tension in the bleb? If this is the case, it indicates that the level of membrane tension has a prominent role in determining the localization of Piezo1. In line with this, it appears more Piezo1 proteins are localized in less tensed tethers.  Thus, might your observations be equally consistent with tension rather than curvature as a key regulator of Piezo1 localization?  We recommend adding this to your discussion.

3. Given the intrinsically curved structure of Piezo1, it is difficult to understand the model’s prediction that curved Piezo1 is not enriched in 25-75 nm invaginations. Where will Piezo1 normally reside in the plasma membrane?  It would be helpful if this could be discussed.

4. It is currently unknown whether and how long Yoda1 might keep Piezo1 in a flattened state. Given that Yoda1 is highly hydrophobic, it might affect membrane properties instead of the curvature of Piezo1.  These caveats should be discussed.

5. The authors state that “Yoda1 leads to a Ca2+ independent increase of Piezo1 on tethers”. It has not been determined yet that Yoda1 leads to Piezo1 flattening (or even opening). In Electrophysiology experiments, unless there is pressure applied, Yoda1 does not lead to substantial currents. Therefore, the cartoon of Yoda1 flattening Piezo1(3H) is misleading. We recommend revising this.  So far, the best experimental evidence on flattening is via purified channels reconstituted in various sizes of liposomes. However, it is plausible that the flattened shape is closed or open inactivated. Because most of the claims of this paper depend on the curved vs flattened shape of Piezo1, the authors should address these caveats carefully.

6. Page 9:  "Our study shows this conformational change of Piezo1 in live cells (Fig. 3H)."  We recommend that this claim be removed as it seems too strong for the provided data.

Additional suggestions for the authors to consider:

1. Based on the calculated spontaneous curvature of Piezo1-membrane C0 of 87 nm, is it possible to derive the curvature of Piezo1 protein itself and the associated membrane footprint?  This would be a nice addition.

2. It is hard to see the filopodia and their localization in the figures.  It would be better for readers and more convincing if clearer/higher resolution example images could be provided.

3. Can the authors better explain how the calculations done in panel 1C and S3D are done and their importance?

4. In Figure 2E, are these data from hPiezo1 or mPiezo1? In other cases, hPiezo1 is specified, this this may be a typo?

5. Figure 3 F&G:  We assume these cells are the same in all panels, just visualized with either mCherry or eGFP in each condition.  Accordingly, we would have expected more swelling in hypotonic conditions, and wonder if further evaluation may resolve this apparent discrepancy? If not, please provide more clarification.

6. On a lighter note, we’d recommend not using in cellulo.

REVIEWING TEAM

Reviewed by:

Alec Nickolls, Postdoctoral Fellow, NCCIH, USA: Piezo structure/function, iPSC cell technologies and disease genetics

Ruhma Syeda, Assistant Professor, University of Texas Southwestern Medical Center, USA: Piezo structure/function, lipids, biochemistry, biophysics

Bailong Xiao, Professor, Tsinghua University, China: Piezo structure/function, cryo-EM, ion channel biophysics, molecular genetics

Curated by:

Alex Chesler, Senior Investigator, NCCIH, USA

(This consolidated report is a result of peer review conducted by Biophysics Colab on version 1 of this preprint. Minor corrections and presentational issues have been omitted for brevity.)

Endorsement statement (5 August 2022)

Peter et al. describe the first experimentally validated structural model of a canonical member of the TRAP family of transporters, Haemophilus influenzae (Hi)SiaPQM, which transports sialic acid into bacteria. By elegantly combining a cryo-EM structure of the HiSiaQM dimer, AlphaFoldmodels, and sequence, biochemical, and mutational analyses, the authors shed light on the fold and domain organization of the tripartite HiSiaPQM holocomplex. The authors also propose a structure-based model for its transport mechanism: substrate recognition is "outsourced" to the substrate binding protein (P protein) by the QM proteins, which in turn use an elevator mechanism to transport sialic acid across the membrane. The work is rigorous and convincing, and it presents valuable findings that will be of interest to scientists investigating transporters with an elevator-type mechanism as well as membrane transport more generally.

(This endorsement by Biophysics Colab refers to the version of record for this work, which is linked to and has been revised from the original preprint following peer review.)

Authors' response (4 August 2022)

GENERAL ASSESSMENT

Tripartite ATP-independent periplasmic transporters (TRAPs) are found in many bacterial and archaeal organisms. Some TRAPs are essential for survival of pathogenic microorganisms (e.g., H. influenzae and V. cholerae). TRAPs are secondary active transporters that couple the uptake of substrate to the symport of two sodium ions. TRAPs have membrane-embedded Q & M domains, and a soluble substrate-binding protein (SBP or P), which captures and delivers substrates to the QM domains. Whereas the structures of some SBPs were known, no structural information was available for the membrane-embedded QM domains of a TRAP transporter.

This manuscript by Peter and colleagues describes the 3D architecture of a canonical member of the TRAP family of transporters, Haemophilus influenzae (Hi)SiaPQM, a sialic acid transporter, using a combination of experimental structures and structure predictions. They determined a cryoEM structure of the transmembrane component, HiSiaQM, in lipid nanodiscs at medium resolution (the actual resolution is unclear in the original version of the manuscript). To overcome the challenge that HiSiaQM has a molecular weight of 70 kDa, too small for straight-forward single-particle Cryo-EM imaging, the authors generated single variable domain on heavy chain (VHH) antibodies, which inhibit the transporter in cell-based assays. They then generate a Megabody using one of them and decorated HiSiaQM to facilitate particle picking and alignment. The authors are cautious in their interpretation of the map and use Alphafold to aid model building. HiSiaQM forms a monomeric elevator-type fold in which the "M" module has homology to the VcINDY substrate-binding domain, and the "Q" module forms an extended stator domain. The HiSiaQM structure is in an inward-open conformation, and they use a structure of VcINDY to predict an outward-open conformation. Using AlphaFold, they also generate a prediction for how the SBP or "P" module, the periplasmic sialic acid binding protein, interacts with the QM transmembrane component. They use a complementation assay to validate aspects of their model by determining the functional consequence of mutations at key positions.

This elegant study combines diverse approaches to develop compelling mechanistic hypotheses. The manuscript provides the first experimentally validated structural model of a full TRAP transporter, shedding light on its fold and domain organization. The new structure and models also allow the authors to propose a more detailed and structure-based working model for its transport mechanism: substrate recognition is "outsourced" to the SBP by QM, which then uses an elevator mechanism to transport sialic acid across the membrane.

The method section is exemplary in detail, and much of the biochemical data (protein preparations and in vitro VHH or sialic acid binding assays) are of high quality. The assay to probe from which side the VHH binders inhibit the transporter is cleverly designed. The cryoEM structure is of medium resolution, but by using predicted folds and homology to other elevator-type transporters, the authors arrive at a well-supported model, although with the current presentation of the data, it is unclear to what extent the model is accurate in its details. The sequence, biochemical, and mutational analyses are not extensive in scope, although they are useful to support the structural model. With the tools and reagents available to the authors, it is somewhat surprising that they used a Megabody instead of the SBP to increase the size of the particles (e.g., it seems that they could use the same SPR assay they used to measure nanobody binding to search for conditions that promote SBP binding to the QM domain). Therefore, an experimental structure of the full HiSiaPQM transporter awaits future studies.

Thank you for this overall positive assessment of our manuscript.

RECOMMENDATIONS

Revisions essential for endorsement:

1. The study's main limitation is the low resolution of the maps and the consequent need to rely on modeling, which likely recapitulates the overall fold well but might fail on details. Therefore, it is important to document how good the model is and how informative the data are in critical protein regions. Specifically, the authors should show close-ups of the model placed into the density for regions such as expected sodium and substrate binding sites. Also, the authors should show the fit of individual TM helices to substantiate the helical register. Submitting the full coordinates to the Protein Data Bank might be inappropriate if there are significant uncertainties about the structure.

We agree. In the meantime, further processing by a combination of RELION and cryoSPARC has significantly improved the quality of our 3D reconstruction. We can now see conclusive density for many aromatic sidechains that confirm the register of the helices. As suggested by the referees, we provide close-up figures with density in the supporting information (Figure S4, S5).

We have included these data in a revised version of Fig.1 in the published article:https://www.nature.com/articles/s41467-022-31907-y

1. A related issue is that the resolution of the cryoEM structure needs to be clarified: it is stated as 6.2 Å in the main text (page 4, line 18) and the methods, but Fig S4c shows the resolution as 6.84 Å, and Table S1 lists it as 4.5 Å. Similarly, the authors should indicate clearly in the main text which map was used for model building: The authors use their low-resolution map for model building (page 4 line 18), but show that they obtain a higher resolution map by subtracting the signal corresponding to lipid nanodisc (Fig. S4 d,e). The authors should also show their subtracted map at higher contour in Fig. S4, it is not possible to judge the quality of the map at present. As mentioned above, a supplementary figure with individual helices fitted into cryo-EM map would be helpful.

As mentioned in the point above, the data has been reprocessed, now using a combination of cryoSPARC and RELION as shown in Figure S3. We used the particle subtracted map for the model building, which has a GSFC resolution of 4.7 Å. This is now clearly stated in the text. The requested figure with individual helices is shown in the published article:https://www.nature.com/articles/s41467-022-31907-y

1. Section "Experimental validation of the tripartite model": The rationale for choosing mutations is not sufficiently explained, i.e., what is the importance of the periplasmic loop? What are the expected interactions between SBP and QM? It would make it clearer to explain the "scoop-loop" model and the expected P-QM interactions at the very beginning of the section.

Thank you for the suggestion. We have now explained the rational for the selection of the mutants directly at the beginning of this section of the manuscript:

"To validate the described structures, we selected 31 residues in regions that we thought are important for the integrity and function of the TRAP transporter, such as the substrate-binding site of the P-domain (I), the extended periplasmic loops of the Q domain (II), the P-QM interface (III and IV), or the assumed sialic acid- and Na+ binding sites at HP1 and HP2 (V) of the QM domains (Figure 5a) (detailed views of the mutation sites are shown in Figure S14 and a sequence alignment of TRAP transporters in Figure S15 and S16). Sites in the periplasmic loops of the Q domain were selected to test for a potential "scoop-loop" mechanism, as found in SBP-dependent ABC transporters 60. The effects of all mutants were analyzed in the above-described SEVY3-based complementation assay."

It would also help to add interpretation of some of the phenotypes (i.e., for mutants D58R, S60R, E172R, R30E, S356Y, E429R). Overall, the discussion of the location these mutations seems underdeveloped. Finally, it would be useful to have an additional panel in Figure 3 (or edited versions of panels a and b) that indicate on the structural models the position of the mutations that impair sialic acid transport.

We have added a discussion of the individual mutants in the main text and have improved Figure 5, so that the structural impact of the mutants can be better judged by the reader. We have included the new Figure in the published article:https://www.nature.com/articles/s41467-022-31907-y

1. All binding and activity measurements should have an estimation of errors (and a description of what the error bars are) and reproducibility verification. All measurements need replicates and corresponding statements in the figure legend or methods.

Done.

1. The authors should carefully review and revise their references as needed. For example, when discussing other elevator-type transporters, the authors should refer the structural papers as those were the papers that established the elevator-type mechanism. Also, the authors should reference the structural study on the outward-facing conformation of DASS transporters (https://elifesciences.org/articles/61350).

The references have been added.

1. Figure S10: it is unclear how the data for VHHQM4 are interpreted as all VHHs binding except for VHHQM5.

This is because VHHQM4 and VHHQM5 bind to the same region of the QM domains and hence mutually exclusive.

Additional suggestions for the authors to consider:

1. The uniqueness of HiSiaPQM could be better emphasized. Isn't it the first example of a monomeric elevator-type transporter?

Indeed. We have now emphasized this a bit more.

1. It might be beneficial to swap the first two sections of the paper and first describe binders selection and characterization, then the rationale for choosing VHHqm3 for structural work, and the resulting structure.

We thought about this a lot, but decided to start the manuscript with a description of the TRAP structure.

1. Since subtraction of the nanodisc signal improved the resolution of the reconstruction, the authors could try masked classification and refinement of the low-resolution map, including trying other software packages for refinement/classification and masking. Generally, several rounds of ab initio/3D classification are often required to obtain a clean particle stack. If the authors did this, they should indicate as such. The authors may also find it useful to adjust the dynamic masking parameters during refinement in cryoSPARC. Membrane proteins seem to not be compatible with cryoSPARC default values and require adjustment. This may result in cleaner, more accurate FSCs.

Thank you for the suggestion. In the meantime, we have reprocessed the dataset and found that 3D classification in RELION improved the particle stack significantly. We performed one round of 3D classification with alignment, then applied a protein mask and performed another round of 3D classification without alignment. The procedure is described in the updated workflow figure S3 which is also pasted above.

For the local refinement in cryoSPARC we used static masks, as is the default of version 3.1. Dynamic masking is to our knowledge not recommended for local refinements.

1. Page 6, the authors title the section "High-affinity VHHs reveal the membrane orientation…": was the membrane orientation a matter of debate? Also, this result is only mentioned in passing in that section. We suggest editing the section title or the section text to make the two more consistent with each other.

While this point was not a matter of debate, there was nevertheless no experimental evidence for it and we thought it worth mentioning. We have removed the statement from the section heading.

1. Page 6 line 16. Can the authors describe the criteria used to adjust the loops if there is no experimental density for the outward-facing conformation?

The geometry of the loops was relaxed using the regularize feature of Coot. This information has been added to the paper.

"The loops connecting elevator and stator domains were adjusted manually using the geometry regularization feature in Coot 49."

1. In the section on the model of the tripartite transport complex (or perhaps in the following section, in which they describe their experimental validation), the authors should mention that the interface of the periplasmic domain with the transmembrane module has the lowest certainty (Figure S3).

Reprocessing of our dataset resulted in a much better-defined density in this region, see above.

(Related to this, on page 10 line 34, and page 11 line 2, the authors use "perfect" and "perfectly" to describe the fit and match of this interface, which seems overstated considering the evidence available.)

True. We have toned the statement down.

Two other statements warrant further discussion: (i) Why do the authors postulate that both lobes of the SBP would remain connected to the QM protein in both the outward-open and inward-open conformation?

In our working hypothesis, the transporter preferably recognizes the closed state of the SBP. For substrate translocation from the SBP to the transporter, both the transporter and the SBP have to open. The hypothesized conformational coupling of SBP and transporter (as shown in Figure 4) is an elegant way of achieving this. After the substrate translocation the SBP will of course dissociate from the transporter.

We have included single molecule microscopy data to the revised manuscript, which further supports our mechanism.

(ii) Can the authors propose any reason why it would be beneficial to have the dimeric SBP oriented as they predict, with one facing away from the membrane?

We used this example as a way of validating the proposed orientation of the P domain on the transporter. The fact that the second monomer of the SBP dimer does not clash into the transporter supports our model. Our model cannot explain the necessity of a dimeric SBP.

1. It could be nice to discuss the inhibitory effect of nanobodies using the structural information. Can SBP still dock when the nanobody is bound, as seen in the structure? Perhaps this is a basis for inhibition of the transporter from the periplasmic side, and could be similar for other binders that inhibit HiSiaPQM?

We now discuss this in the manuscript. Indeed, the inhibitory effect of VHHQM3 can be explained by our structure because it blocks the SBP binding site and interlocks the stator and elevator domains of the transporter.

1. From Figure 1D and S7, it is difficult to judge how similar are vcINDY and HiSiaPQM in detail around HP1 and HP2. Thus, the conclusion that sodium ions likely bind between the HPs seems unsubstantiated. A focused representation of the structural alignment around the proposed sites and discussion of the relevant residues and their conservation might strengthen the hypothesis.

This has been done in the new Figure 2 in the published article: https://www.nature.com/articles/s41467-022-31907-y

(This is a response to peer review conducted by Biophysics Colab on version 1 of this preprint.)

Consolidated peer review report (19 February 2022)

GENERAL ASSESSMENT

Tripartite ATP-independent periplasmic transporters (TRAPs) are found in many bacterial and archaeal organisms. Some TRAPs are essential for survival of pathogenic microorganisms (e.g., H. influenzae and V. cholerae). TRAPs are secondary active transporters that couple the uptake of substrate to the symport of two sodium ions. TRAPs have membrane-embedded Q & M domains, and a soluble substrate-binding protein (SBP or P), which captures and delivers substrates to the QM domains. Whereas the structures of some SBPs were known, no structural information was available for the membrane-embedded QM domains of a TRAP transporter.

This manuscript by Peter and colleagues describes the 3D architecture of a canonical member of the TRAP family of transporters, Haemophilus influenzae (Hi)SiaPQM, a sialic acid transporter, using a combination of experimental structures and structure predictions. They determined a cryoEM structure of the transmembrane component, HiSiaQM, in lipid nanodiscs at medium resolution (the actual resolution is unclear in the original version of the manuscript). To overcome the challenge that HiSiaQM has a molecular weight of 70 kDa, too small for straight-forward single-particle Cryo-EM imaging, the authors generated single variable domain on heavy chain (VHH) antibodies, which inhibit the transporter in cell-based assays. They then generate a Megabody using one of them and decorated HiSiaQM to facilitate particle picking and alignment. The authors are cautious in their interpretation of the map and use Alphafold to aid model building. HiSiaQM forms a monomeric elevator-type fold in which the “M” module has homology to the VcINDY substrate-binding domain, and the “Q” module forms an extended stator domain. The HiSiaQM structure is in an inward-open conformation, and they use a structure of VcINDY to predict an outward-open conformation. Using AlphaFold, they also generate a prediction for how the SBP or “P” module, the periplasmic sialic acid binding protein, interacts with the QM transmembrane component. They use a complementation assay to validate aspects of their model by determining the functional consequence of mutations at key positions.

This elegant study combines diverse approaches to develop compelling mechanistic hypotheses. The manuscript provides the first experimentally validated structural model of a full TRAP transporter, shedding light on its fold and domain organization. The new structure and models also allow the authors to propose a more detailed and structure-based working model for its transport mechanism: substrate recognition is “outsourced” to the SBP by QM, which then uses an elevator mechanism to transport sialic acid across the membrane.

The method section is exemplary in detail, and much of the biochemical data (protein preparations and in vitro VHH or sialic acid binding assays) are of high quality. The assay to probe from which side the VHH binders inhibit the transporter is cleverly designed. The cryoEM structure is of medium resolution, but by using predicted folds and homology to other elevator-type transporters, the authors arrive at a well-supported model, although with the current presentation of the data, it is unclear to what extent the model is accurate in its details. The sequence, biochemical, and mutational analyses are not extensive  in scope, although they are useful to support the structural model. With the tools and reagents available to the authors, it is somewhat surprising that they used a Megabody instead of the SBP to increase the size of the particles (e.g., it seems that they could use the same SPR assay they used to measure nanobody binding to search for conditions that promote SBP binding to the QM domain). Therefore, an experimental structure of the full HiSiaPQM transporter awaits future studies.  

RECOMMENDATIONS

Revisions essential for endorsement:

1. The study's main limitation is the low resolution of the maps and the consequent need to rely on modeling, which likely recapitulates the overall fold well but might fail on details. Therefore, it is important to document how good the model is and how informative the data are in critical protein regions. Specifically, the authors should show close-ups of the model placed into the density for regions such as expected sodium and substrate binding sites. Also, the authors should show the fit of individual TM helices to substantiate the helical register. Submitting the full coordinates to the Protein Data Bank might be inappropriate if there are significant uncertainties about the structure.

2. A related issue is that the resolution of the cryoEM structure needs to be clarified: it is stated as 6.2 Å in the main text (page 4, line 18) and the methods, but Fig S4c shows the resolution as 6.84 Å, and Table S1 lists it as 4.5 Å. Similarly, the authors should indicate clearly in the main text which map was used for model building: The authors use their low-resolution map for model building (page 4 line 18), but show that they obtain a higher resolution map by subtracting the signal corresponding to lipid nanodisc (Fig. S4 d,e). The authors should also show their subtracted map at higher contour in Fig. S4, it is not possible to judge the quality of the map at present. As mentioned above, a supplementary figure with individual helices fitted into cryo-EM map would be helpful.

3. Section “Experimental validation of the tripartite model”: The rationale for choosing mutations is not sufficiently explained, i.e., what is the importance of the periplasmic loop? What are the expected interactions between SBP and QM? It would make it clearer to explain the “scoop-loop” model and the expected P-QM interactions at the very beginning of the section. It would also help to add interpretation of some of the phenotypes (i.e., for mutants D58R, S60R, E172R, R30E, S356Y, E429R). Overall, the discussion of the location these mutations seems underdeveloped. Finally, it would be useful to have an additional panel in Figure 3 (or edited versions of panels a and b) that indicate on the structural models the position of the mutations that impair sialic acid transport.

4. All binding and activity measurements should have an estimation of errors (and a description of what the error bars are) and reproducibility verification. All measurements need replicates and corresponding statements in the figure legend or methods.

5. The authors should carefully review and revise their references as needed. For example, when discussing other elevator-type transporters, the authors should refer the structural papers as those were the papers that established the elevator-type mechanism. Also, the authors should reference the structural study on the outward-facing conformation of DASS transporters (https://elifesciences.org/articles/61350).

6. Figure S10: it is unclear how the data for VHHQM4 are interpreted as all VHHs binding except for VHHQM5.

Additional suggestions for the authors to consider:

1. The uniqueness of HiSiaPQM could be better emphasized. Isn’t it the first example of a monomeric elevator-type transporter?

2. It might be beneficial to swap the first two sections of the paper and first describe binders selection and characterization, then the rationale for choosing VHHqm3 for structural work, and the resulting structure.

3. Since subtraction of the nanodisc signal improved the resolution of the reconstruction, the authors could try masked classification and refinement of the low-resolution map, including trying other software packages for refinement/classification and masking. Generally, several rounds of ab initio/3D classification are often required to obtain a clean particle stack. If the authors did this, they should indicate as such. The authors may also find it useful to adjust the dynamic masking parameters during refinement in cryoSPARC. Membrane proteins seem to not be compatible with cryoSPARC default values and require adjustment. This may result in cleaner, more accurate FSCs.

4. Page 6, the authors title the section “High-affinity VHHs reveal the membrane orientation…”: was the membrane orientation a matter of debate? Also, this result is only mentioned in passing in that section. We suggest editing the section title or the section text to make the two more consistent with each other.

5. Page 6 line 16. Can the authors describe the criteria used to adjust the loops if there is no experimental density for the outward-facing conformation?

6. In the section on the model of the tripartite transport complex (or perhaps in the following section, in which they describe their experimental validation), the authors should mention that the interface of the periplasmic domain with the transmembrane module has the lowest certainty (Figure S3). (Related to this, on page 10 line 34, and page 11 line 2, the authors use “perfect” and “perfectly” to describe the fit and match of this interface, which seems overstated considering the evidence available.) Two other statements warrant further discussion: (i) Why do the authors postulate that both lobes of the SBP would remain connected to the QM protein in both the outward-open and inward-open conformation? (ii) Can the authors propose any reason why it would be beneficial to have the dimeric SBP oriented as they predict, with one facing away from the membrane?

7. It could be nice to discuss the inhibitory effect of nanobodies using the structural information. Can SBP still dock when the nanobody is bound, as seen in the structure? Perhaps this is a basis for inhibition of the transporter from the periplasmic side, and could be similar for other binders that inhibit HiSiaPQM?

8. From Figure 1D and S7, it is difficult to judge how similar are vcINDY and HiSiaPQM in detail around HP1 and HP2. Thus, the conclusion that sodium ions likely bind between the HPs seems unsubstantiated. A focused representation of the structural alignment around the proposed sites and discussion of the relevant residues and their conservation might strengthen the hypothesis.

REVIEWING TEAM

Reviewed by:

Olga Boudker, Professor and HHMI Investigator, Weill Cornell Medicine, USA: structure and mechanism of membrane transporters

Rachelle Gaudet, Professor, Harvard University, USA: structure and mechanisms of transporters

Valeria Kalienkova, Postdoctoral Researcher (C. Paulino lab, University of Groningen, Netherlands): single particle cryo-EM, x-ray crystallography, membrane proteins

Krishna Reddy, Postdoctoral Researcher (O. Boudker lab, Weill Cornell Medicine, USA): single-particle cryo-EM, membrane protein structure and mechanism

Curated by:

Rachelle Gaudet, Professor, Harvard University, USA

(This consolidated report is a result of peer review conducted by Biophysics Colab on version 1 of this preprint. Minor corrections and presentational issues have been omitted for brevity.)

Endorsement statement (28 June 2022)

Sauer et al. describe two cryo-EM structures of the Na⁺-dependent dicarboxylate transporter VcINDY in two inward-facing states. The high-quality structural data, complemented by NMR-inspired analysis, functional assays and cysteine accessibility measurements, reveal crucial conformational changes induced by Na⁺ binding to apo VcINDY that result in formation of the substrate-binding site. This is a strong manuscript that provides an important contribution to our understanding of the transport mechanism in the SLC13/DASS family of transporters, several members of which have critical physiological functions. The work will be of interest to researchers working on this and other ion-coupled transporter families.

(This endorsement by Biophysics Colab refers to the version of record for this work, which is linked to and has been revised from the original preprint following peer review.)

Consolidated peer review report (2 June 2022)

GENERAL ASSESSMENT

Xu et al. report a new protein engineering strategy to obtain cryo-EM structures of group-A GPCRs in non-G protein-bound forms (apo, agonist or antagonist bound). Class-A GPCRs are 7 transmembrane helical proteins that are completely membrane-embedded with no prominent structural features outside the membrane limits. This topology makes particle alignment extremely difficult in the cryo-EM data processing workflow. Therefore, cryo-EM structures of GPCRs have typically been determined by coupling the receptors to G proteins or arrestins. However, this approach limits the information obtained about different functional states, particularly the inactive state.

To address this fundamental issue, the authors attach calcineurin, a heterodimeric protein composed of CN-A and CN-B subunits, to the β2 adrenergic receptor (β2AR) protein. The attachment is made through a three-point fusion to the cytoplasmic ends of TM5, TM6, and TM7, providing a rigid anchor to the coupled protein. They show that this strategy can be used as a potential tool (as a rigid fiducial marker) for aiding particle alignment of small GPCR proteins. To obtain a resolution of 3.5 Å, they shorten the linkers and use an additional protein binder (FKBP12) and a compound (Tacrolimus).

As a summary, this work brings novel strategies to determine cryo-EM structures of GPCRs in inactive states and bound to pharmacologically relevant antagonists and/or partial agonists (or any other agonists) that cannot be stabilized with a Gabg heterotrimer. These strategies could be extended to the less understood orphan receptors, where at times an agonist is not available, and to structural studies on negative allosteric modulators or novel types of antagonistic modulators.  Together with the pre-existing nanobodies and scFvs available for GPCRs, there are exciting times ahead where innovative ways of using these tools can lead to novel insights into GPCR functionality and therapeutic modulation. Beyond GPCRs, the approach to fuse a heterodimeric protein to the protein of interest to increase the mass as well as resolve particle alignment issues could be adapted for structure determination of small, symmetrical membrane proteins.

RECOMMENDATIONS

Revisions essential for endorsement:

1.     There are two additional strategies that have been proposed to achieve a similar goal (the use of a universal nanobody binding intracellular loop 3 (ICL3) and fusion of a rigid BRIL to TM5-6). The universal nanobody strategy has led to structures of small membrane proteins and to inactive states of GPCRs at good resolution (ranging from 2.4 - 3.1 Å). It would be helpful if the authors were to discuss this issue in light of other protein engineering methods and provide some directions to further optimize the CN-fusion method to obtain higher resolutions.

2.     Some limitations of the new strategy arise from the need to optimize for each receptor, although it seems that any engineering would be restricted to finding suitable length linkers. However, it was not clear to the reviewers whether calcineurin interacts with the cytoplasmic end of the receptor. The authors compare the helical folding of ICL2 in cryo-EM structures with X-ray crystallographic structures, however, it is unclear from the figures whether ICL2 interacts with calcineurin. Additionally, it seems the receptors fused to calcineurin are stabilized in an inactive state, as a slightly detrimental effect on agonist affinity is seen. Although the authors suggest this might be due to the short linkers, this could also be due to the interaction of calcineurin with the intracellular side (if it does interact). It would be good to clarify this in the revision.

Additional suggestions for the authors to consider:

1.     The distance between TM5 and TM6 of β2AR is 11 Å. Do the authors think this distance has facilitated the incorporation of calcineurin into β2AR? Could this be a problem for small membrane proteins in which fusing a heterodimeric protein to the loop region might introduce steric clashes?

2.     The authors should mention the BRIL strategy used to obtain structures of GPCRs without coupling to G proteins (Zhang, bioRxiv, 2021).

REVIEWING TEAM

Reviewed by:

Sayan Chakraborty, Postdoctoral Associate, Weill Cornell Medicine, USA: membrane protein biochemistry, X-ray crystallography

Javier Garcia-Nafria, Researcher, University of Zaragoza, Spain: cryo-electron microscopy, G protein-coupled receptors

Curated by:

Sudha Chakrapani, Professor, Case Western Reserve University, USA

(This consolidated report is a result of peer review conducted by Biophysics Colab on version 1 of this preprint. Minor corrections and presentational issues have been omitted for brevity.)

Consolidated peer review report (23 November 2021)

GENERAL ASSESSMENT

Transport of metabolites across the mitochondrial inner membrane is a vital process which sustains the metabolic pathways connecting mitochondria and cytosol. Approximately one-third of the mitochondrial carriers of the SLC25 family, consisting of 53 members, are currently orphan transporters, limiting our understanding of mitochondrial transport and mitochondrial metabolism. This preprint reports a combinatorial CRISPR screening approach to probe interactions between mitochondrial carriers and their dependence on the metabolic environment, comparing different metabolic states of the cell and conditions under which mitochondrial respiration is or is not required. This is a potentially powerful approach to facilitate the identification of orphan transporters.

The authors identify a number of gene-by-gene, gene-by-environment and gene-by-gene-environment interactions. They confirm known functions of previously identified carriers, and they analyze gene-by-environment interactions of the proposed mitochondrial folate carrier, SLC25A32. A main highlight of this study is the conclusion that the orphan carrier SLC25A39 is involved in glutathione transport. Glutathione is a very important metabolite which plays a key role in protecting mitochondria against oxidative damage but the carrier responsible for this function remained undefined. Building on a strong observed interaction with a known iron transporter, the authors performed mitochondrial metabolite profiling where they observed depletion of both the reduced and the oxidized glutathione in mitochondria of the SLC25A39 knockout, while no changes were observed in the whole cell glutathione content. Additionally, they reported reduced glutathione transport in the mitochondria of the knockout compared to control and site directed mutagenesis in residues predicted via homology modeling to be part of the substrate binding site. Altogether, the study provides strong evidence on the importance of SLC25A39 in mitochondrial transport of glutathione and therefore it is an important contribution in the fields of mitochondrial transport, metabolism, physiology, and medicine.

The dual Cas9 screening approach employed here brings an important innovation to the study of mitochondrial carriers, which have traditionally been difficult to identify due to considerable functional redundancy. The screening in different media conditions has highlighted links that would have remained unidentified in a single medium, and the use of knockout pairs can overcome issues relevant to functional redundancy of the carriers. It is evident that this approach can provide a wealth of testable ideas on the physiological role of mitochondrial carriers and could provide a framework for exciting future studies on the identification of other orphan transporters in mitochondria. A strength of this study that this approach provides strong support for a role for SLC25A39 in glutathione transport, as also proposed by an independent study by Wang et al (2021) Nature 599, 136-140. The findings presented here provide strong motivation for undertaking in vitro reconstitution experiments to definitively demonstrate that SLC25A39 is a glutathione transporter.

Beyond the novel finding on the involvement of SLC25A39 in glutathione transport, the authors showcase the usefulness of their combinatorial CRISPR screen on the SLC25A19 and SLC25A32 carriers and the paralogous genes encoding the mitochondrial ADP/ATP carriers. In this part of the study, which covers half of the manuscript, they provide many interesting observations and raise a few questions. For example, they find no fitness defect for the SLC25A32 KO in galactose, which could imply that this carrier does not transport FAD as previously proposed or alternatively, there could be a redundant mechanism. Another example is that they propose there could be functional differences between the ADP/ATP carriers. These efforts are admirable, and we can appreciate it was challenging to combine the methodological validation of the CRISPR screen and a new functional identification in a single manuscript, but these unresolved issues do leave the reader wanting to know more.

RECOMMENDATIONS

Revisions essential for endorsement:

Experiments:

1) If the authors could report the difference in the initial rates of glutathione transport between SLC25A39 KO and control in isolated mitochondria, it would strengthen the conclusion that SLC25A39 is a glutathione transporter. To calculate this accurately, the authors would need collect more time points in the first five minutes of the time course. It is also not clear, and should be indicated, against which protein they normalize their data.

Discussion:

1) A gene-by-gene buffering interaction has been identified between SLC25A39 and SLC25A37, an iron transporter, in all four media conditions, with the strongest in antimycin. As this is an important observation powered by the combinatorial screen approach, a further discussion seems warranted. Although the link between glutathione and iron metabolism is obvious and known, it is not clear why this would be a buffering interaction. Could the authors provide a specific metabolic explanation for these data?

2) The recent study by Wang et al., is associating SLC25A39, but also SLC25A40, with glutathione transport. It would be helpful to the reader if the authors could discuss this finding in the context of their results.

3) As the highlight of the manuscript relates to glutathione transport, more background information on glutathione, its role in metabolism and pathophysiology and previous attempts to identify this carrier would be helpful for the reader.

4) Please discuss the debate around SLC25A32 function in the text more deliberately as convincing molecular experimental evidence on its substrate is still lacking.

Additional suggestions for the authors to consider:

1) In vitro studies can prove unequivocally that SLC25A39 is the mitochondrial glutathione transporter. This manuscript will have an advantage if the authors can show in an in vitro system that SLC25A39 can transport glutathione.

2) Previous studies had proposed that mitochondrial dicarboxylate and 2-oxoglutarate carriers can transport glutathione, although this has been disputed. Could the authors discuss how the results of this screen relate to these carriers?

3) Why is there a growth defect for the SLC25A19 KO in the -pyruvate condition (Supplementary Figure 2)?

4) Given the significant number of still unidentified mitochondrial carriers, it is somewhat surprising that more interactions with uncharacterized carriers were not identified here. This is likely due to the limited number of media conditions used in the study and could be considered in design of future studies.

REVIEWING TEAM

Reviewed by:

Nora Kory, Assistant Professor, Harvard School of Public Health, USA: functional identification of mitochondrial transporters using metabolite profiling and functional genomics approaches

Sotiria Tavoulari, Research Associate, University of Cambridge, UK: molecular mechanisms of transport, mitochondrial transport, mitochondrial carriers (SLC25), mitochondrial pyruvate carrier (SLC54)

Curated by:

Merritt Maduke, Associate Professor, Stanford University School of Medicine, USA

(This consolidated report is a result of peer review conducted by Biophysics Colab on version 1 of this preprint. Minor corrections and presentational issues have been omitted for brevity.)

Biophysics Colab

Endorsement statement (11 May 2022)

Falzone et al. report important new cryo-EM structures of the fungal calcium-activated lipid scramblase afTMEM16, as well as the functional impact of mutations and different lipid membrane compositions on lipid scrambling. Individual lipids are beautifully resolved around the subunit cavity involved in lipid scrambling in one of the highest resolution structures of a TMEM16 protein solved to date, enabling the role of these lipid-interacting residues to be interrogated. Collectively, the results suggest that afTMEM16 catalyzes lipid scrambling by thinning the membrane rather than providing a hydrophilic permeation pathway for lipids. The work represents an important contribution that will be of interest to scientists investigating the mechanisms of lipid scrambling and how membrane proteins interact with their lipid environment.

(This endorsement by Biophysics Colab refers to the version of record for this work, which is linked to and has been revised from the original preprint following peer review.)

Consolidated peer review report (16 February 2022)

GENERAL ASSESSMENT

The manuscript titled "Structural basis of ion–substrate coupling in the Na+-dependent dicarboxylate transporter VcINDY" by Sauer et al. is an elegant study that details the subtle structural changes of an important secondary-active transporter, VcINDY, upon binding of the co-transported Na+ ions and substrate.  The objective of this study was to identify mechanism(s) underlying substrate and ion coupling in the SLC13/DASS transporter family, for which VcINDY serves as prototype and structural model.  This is important as several members of the SLC13 family have critical physiological functions, which, when disrupted, can lead to disease in humans.

This study describes two cryo-EM structures of the Na+-dependent dicarboxylate transporter VcINDY. The key finding is the structure of the inward-apo state (i.e. in the absence of bound Na+ and substrate) of VcINDY, described for the first time. The second structure of the inward-Na+ bound state has an improved resolution of 2.8 Å, allowing better assignment of Na+ at the Na1 and Na2 sites. Together with intrinsic fluorescence measurements, NMR experiments and a cysteine alkylation assay, the study unveils the crucial conformational changes induced by Na+ binding to apo VcINDY and the formation of the substrate-binding site, adding a critical missing piece to the puzzle.

This is a strong manuscript, which will contribute to our understanding of the SLC13/ DASS family transport mechanism.  The structural data are of high quality, and the resolution is in a range that allows precise mechanistic conclusions, down to the identification of a water cluster at the domain interface.  The data are presented well, and the manuscript is well-written and easy to read. 

One area for improvement in the manuscript concerns the use of the term "induced fit" to describe what is essentially cooperativity.  Our understanding of the manuscript is that “induced fit” is used to describe the mechanism whereby the binding of sodium ion(s) induces the fit of dicarboxylate in the substrate binding site.  If this interpretation of the manuscript is correct, it does not align with the traditional meaning of the "induced fit" hypothesis, as put forward by Koshland.  In this traditional view, induced fit means that the substrate itself, upon initial binding, changes the structure of its own binding site, to provide better correspondence between the shape and intermolecular interactions of the substrate–binding site complex.  In the present manuscript, it is evident that this is the case for Na+ binding (i.e. there is substantial flexibility in the Na+ binding site in the apo state, which decreases upon Na+ binding), whereas the situation is less clear for the dicarboxylate substrate.

RECOMMENDATIONS

Revisions essential for endorsement:

1) We suggest that a more traditional term for describing the formation of the substrate binding site in response to Na+ binding is “cooperativity” of Na+/substrate coupling.  There is clearly cooperativity, in the sense that Na+ binding dramatically increases the affinity for substrate, as has been observed for many other Na+-coupled transporters, including those of the SLC1 family, which somewhat share the general elevator transport mechanism with VcINDY. We suggest that the authors rephrase this description, or at least acknowledge the traditional description of “induced fit” mechanism by Koshland (including reference) and clarify the language regarding cooperativity/induced fit models.

2) In the NMR–style analysis, how many separate refinement runs were performed for the Na+ and Apo structures?

3) Page 7, Results:  "VcINDY was found to bind succinate with a Kd of..."  This is not a Kd value.  The Kd indicates the actual dissociation constant.  This value is rather an apparent Km, which is affected by other processes in the transport cycle, in addition to substrate binding.

Additional suggestions for the authors to consider:    

1) In the intrinsic fluorescence assay, insignificant fluorescence change was observed when succinate was titrated to VcINDY without Na+ (Supplementary Fig.2c). To exclude the possibility that VCINDY purified in ChCl does not respond to succinate addition because of loss of protein function during purification, it would be nice to show a positive control. One suggestion is to add NaCl to VcINDY in ChCl, after titration of 1000 μM succinate. A significant fluorescence change comparable to Supplementary Fig.2b would be expected for a positive control. In addition, does the addition of Na+ alone (without succinate) to VcINDY in ChCl cause any fluorescence change? It would be interesting to show.

2) As noted in the manuscript, 3 Na+ ions are co-transported with succinate. In the improved Na+-bound VcINDY structure reported in this study, the Na1 and Na2 sites are well resolved. Asking out of curiosity, do the authors have any thoughts on where Na3 is located on the Na+-bound structure given the data available? In the induced-fit mechanism proposed in the manuscript, are all 3 Na+ ions believed to bind to the Apo transporter before succinate binding?

3) It is noted that four 3D classes are generated from the VcINDY-choline cryo-EM dataset. The highest resolution class was further refined to 3.2 Å. The resolutions of the remaining three classes are between 3.8 Å and 4.4 Å. May the authors briefly describe what do the other three classes look like? Do they all resemble the same conformation? Also, since the transporter is a homodimer and each monomer might function independently, refining the dimer as a whole might not be enough to resolve potential heterogeneous states in the dataset. May the authors discuss if they have tried symmetry expansion and focused 3D classification on one protomer to look for different states, especially in the Apo dataset which may have high heterogeneity? In addition, 3D variability analysis might also be helpful to show the flexibility of the Apo structure.

REVIEWING TEAM

Reviewed by:

Christof Grewer, Professor, Binghamton University USA: transport mechanisms, kinetics, and structure/function of secondary-active transporters

Renae M. Ryan, Professor, University of Sydney, Australia: structure and function of membrane transporters

Xiaoyu Wang, Instructor (O. Boudker lab), Cornell University, USA: membrane transporters, structural biology

Curated by:

Renae M. Ryan, Professor, University of Sydney, Australia

(This consolidated report is a result of peer review conducted by Biophysics Colab on version 1 of this preprint. Minor corrections and presentational issues have been omitted for brevity.)

Authors' response (4 May 2022)

GENERAL ASSESSMENT

The manuscript titled "Structural basis of ion–substrate coupling in the Na+-dependent dicarboxylate transporter VcINDY" by Sauer et al. is an elegant study that details the subtle structural changes of an important secondary-active transporter, VcINDY, upon binding of the co-transported Na+ ions and substrate. The objective of this study was to identify mechanism(s) underlying substrate and ion coupling in the SLC13/DASS transporter family, for which VcINDY serves as prototype and structural model. This is important as several members of the SLC13 family have critical physiological functions, which, when disrupted, can lead to disease in humans.

This study describes two cryo-EM structures of the Na+-dependent dicarboxylate transporter VcINDY. The key finding is the structure of the inward-apo state (i.e. in the absence of bound Na+ and substrate) of VcINDY, described for the first time. The second structure of the inward-Na+ bound state has an improved resolution of 2.8 Å, allowing better assignment of Na+ at the Na1 and Na2 sites. Together with intrinsic fluorescence measurements, NMR experiments and a cysteine alkylation assay, the study unveils the crucial conformational changes induced by Na+ binding to apo VcINDY and the formation of the substrate-binding site, adding a critical missing piece to the puzzle.

This is a strong manuscript, which will contribute to our understanding of the SLC13/ DASS family transport mechanism. The structural data are of high quality, and the resolution is in a range that allows precise mechanistic conclusions, down to the identification of a water cluster at the domain interface. The data are presented well, and the manuscript is well-written and easy to read.

One area for improvement in the manuscript concerns the use of the term "induced fit" to describe what is essentially cooperativity. Our understanding of the manuscript is that "induced fit" is used to describe the mechanism whereby the binding of sodium ion(s) induces the fit of dicarboxylate in the substrate binding site. If this interpretation of the manuscript is correct, it does not align with the traditional meaning of the "induced fit" hypothesis, as put forward by Koshland. In this traditional view, induced fit means that the substrate itself, upon initial binding, changes the structure of its own binding site, to provide better correspondence between the shape and intermolecular interactions of the substrate–binding site complex. In the present manuscript, it is evident that this is the case for Na+ binding (i.e. there is substantial flexibility in the Na+ binding site in the apo state, which decreases upon Na+ binding), whereas the situation is less clear for the dicarboxylate substrate.

We are grateful to colleagues from Biophysics Colab for reviewing our manuscript. We have revised the manuscript according to their suggestions, along with later revision based on comments from the publishing journal's reviewers. The revised manuscript is stronger and sharper, and we have explicitly thanked the help from Biophysics Colab in the acknowledgement section.

RECOMMENDATIONS Revisions essential for endorsement:

We suggest that a more traditional term for describing the formation of the substrate binding site in response to Na+ binding is "cooperativity" of Na+/substrate coupling. There is clearly cooperativity, in the sense that Na+ binding dramatically increases the affinity for substrate, as has been observed for many other Na+-coupled transporters, including those of the SLC1 family, which somewhat share the general elevator transport mechanism with VcINDY. We suggest that the authors rephrase this description, or at least acknowledge the traditional description of "induced fit" mechanism by Koshland (including reference) and clarify the language regarding cooperativity/induced fit models.

We appreciate the reviewer's highlighting the correct nomenclature to describe our observed sodium-dependent substrate binding. We have revised the manuscript, explicitly stating the "cooperativity" of Na+ and succinate binding. We have also cited a review by Hammes et al (PNAS, 2009) that compares the induced-fit and conformational selection mechanisms.

In the NMR–style analysis, how many separate refinement runs were performed for the Na+ and Apo structures?

Each NMR-style analysis used 5 independent runs with NCS turned off, generating 10 independent models. This is been explicitly stated in the revised text, and we appreciate the reviewer's reminder to note this detail.

Page 7, Results: "VcINDY was found to bind succinate with a Kd of..." This is not a Kd value. The Kd indicates the actual dissociation constant. This value is rather an apparent Km, which is affected by other processes in the transport cycle, in addition to substrate binding.

We agree with the reviewer that the measured succinate binding may not represent the true Kd for succinate binding, being influenced by other processes in the transporter's conformational cycle. However, the relationship between substrate induced protein changes in vitro versus in vivo is not known. Therefore, we disagree about describing this value as Km, which is the concentration for 50% enzymatic activity rate. We are not measuring directly or indirectly the enzyme turnover (transport rate) in this experiment, and therefore the term Km would be misleading. To better reflect the difference between our in vitro measurement and the biological binding process, we have modified the text to describe it as an "apparent Kd".

Additional suggestions for the authors to consider:

In the intrinsic fluorescence assay, insignificant fluorescence change was observed when succinate was titrated to VcINDY without Na+ (Supplementary Fig.2c). To exclude the possibility that VCINDY purified in ChCl does not respond to succinate addition because of loss of protein function during purification, it would be nice to show a positive control. One suggestion is to add NaCl to VcINDY in ChCl, after titration of 1000 μM succinate. A significant fluorescence change comparable to Supplementary Fig.2b would be expected for a positive control. In addition, does the addition of Na+ alone (without succinate) to VcINDY in ChCl cause any fluorescence change? It would be interesting to show.

The reviewers raise an important caveat regarding the choline binding experiment, and possible control experiment. In ongoing studies, we have performed a similar experiment, measuring Na+ binding for VcINDY purified in choline. Notably, VcINDY's apparent Kd for Na+ is very similar to the previously reported K0.5 in proteoliposomes (Mulligan, JGP, 2014). This indicates VcINDY purified in choline remains properly folded and functional, and the results will be reported in a follow-up study.

As noted in the manuscript, 3 Na+ ions are co-transported with succinate. In the improved Na+- bound VcINDY structure reported in this study, the Na1 and Na2 sites are well resolved. Asking out of curiosity, do the authors have any thoughts on where Na3 is located on the Na+-bound structure given the data available? In the induced-fit mechanism proposed in the manuscript, are all 3 Na+ ions believed to bind to the Apo transporter before succinate binding?

The binding site for Na3, and its placement in the substrate binding sequence, is the focus of on-going studies in the lab. However, in previous studies of the homologous human transporter NaDC-1 all Na+ ions were found to bind prior to substrate binding, with the sequence reversed for the release of substrate and sodium. Therefore, the manuscript has been revised to note the unknown role of Na3 in VcINDY's sodium-induced structural changes.

It is noted that four 3D classes are generated from the VcINDY-choline cryo-EM dataset. The highest resolution class was further refined to 3.2 Å. The resolutions of the remaining three classes are between 3.8 Å and 4.4 Å. May the authors briefly describe what do the other three classes look like? Do they all resemble the same conformation?

The four, low resolution C1 maps of VcINDY in choline all have distinctly weakened density for HPin and TM10b. However, this varies between maps and protomers, indicating these regions of the protein are in an ensemble of conformations. We have included these maps in the revised manuscript (Supplementary Fig. 7) to illustrate this variation.

Also, since the transporter is a homodimer and each monomer might function independently, refining the dimer as a whole might not be enough to resolve potential heterogeneous states in the dataset. May the authors discuss if they have tried symmetry expansion and focused 3D classification on one protomer to look for different states, especially in the Apo dataset which may have high heterogeneity? In addition, 3D variability analysis might also be helpful to show the flexibility of the Apo structure.

The reviewers pose an interesting possibility of processing the VcINDY-choline dataset using more sophisticated techniques to resolve the heterogeneous structures within the Ci-apo state. While we refined the model initially with C1 symmetry to begin to address this prospect, as discussed, we are hesitant to attempt much further. The mobile region in VcINDY is much smaller than targets that have previously undergone this sort of analysis. However, we have deposited the particle stacks into EMDB to enable software development and validation on such challenging cases.

(This is a response to peer review conducted by Biophysics Colab on version 1 of this preprint.)

Endorsement statement (27 April 2022)

The preprint by Fiedorczuk and Chen presents structures of the cystic fibrosis transmembrane conductance regulator (CFTR) chloride channel in complex with type I correctors, a class of drug currently used to treat cystic fibrosis by targeting CFTR folding and stability. The strength of the paper lies in the consistency of the structural data with maturation and binding assays, as well as with much of the existing literature. Overall, the work represents a rigorous investigation of the mechanism of these drugs, and will be of interest to those who study cystic fibrosis, protein folding, and drug design.

(This endorsement refers to version 1 of this preprint, which was peer reviewed by Biophysics Colab.)

Consolidated peer review report (6 April 2022)

GENERAL ASSESSMENT

The sweet and umami sensor proteins, taste receptors type 1 (T1Rs) are important GPCRs underlying taste sensation. In humans, amino acids bind and activate the T1r1/3 heterodimeric receptors leading to umami taste perception, whereas sugars activate the T1r2/3 receptors leading to sweet taste perception. In this manuscript, Atsumi and colleagues combine structural, biophysical and electrophysiological methods to show that Cl- ions also bind to T1Rs, at low mM concentrations, to evoke taste sensation. The authors (1) identify a putative evolutionarily conserved Cl- binding site in the crystal structures of isolated LBDs from medaka fish T1r2a/3 receptors, (2) show that Cl- ions promote protein stability and induce conformational changes in these mfT1r2a/3 LBDs, independent of orthosteric ligands, and (3) demonstrate that mouse chorda tympani nerves are activated by Cl- ions via a T1R-specific mechanism. Based on these findings, the authors conclude that low concentrations of Cl- may bind to sweet receptors and mediate the commonly reported sweet taste sensation following ingestion of low concentrations of table salt.

The elucidation of the molecular mechanism(s) underlying salt taste sensation is a physiologically relevant question that will appeal to a broad audience. Moreover, the authors use an impressive array of different approaches to broadly cover numerous aspects, ranging from structural biology, to biophysics and physiological recordings. Overall, the identification of the chloride ion binding site is convincing, based on the previously solved structure, as well as the bromide ion substitution and long-wavelength Cl- anomalous difference analysis performed in this work. This analysis is supported by biophysical measurements showing that Cl- substantially stabilizes the wild type complex against thermal denaturation, but does not stabilize a point mutant in the putative Cl- binding site. The single fiber recordings suggest there is physiological relevance to the biophysical and structural findings, although they could be strengthened by additional control experiments. Overall, the possibility of Cl- ions acting as a sweet receptor ligand is enticing and the work will likely motivate additional research on this subject.

RECOMMENDATIONS

Revisions essential for endorsement:

1) The authors should provide refinement statistics and methodology for both the Cl-- and Br-- bound structures, and some comparison between these two structures (global structural alignment & RMSD should be sufficient).

2) We would recommend that the authors perform nerve recordings using artificial saliva rather than water as the perfusate.  This is a key point because the chloride concentration in saliva is approximately 15 mM. Thus, according to their binding data, most T1rs should have chloride bound at baseline. Perhaps this means that chloride binding is required to allow sucrose or other ligands to cause sufficient conformational changes and receptor activation?  If this is the mechanism, it would still be quite interesting, but would change the framing/interpretation as presented in the manuscript. If additional experiments are not feasible, the authors should carefully discuss this point.

3) Some of the conclusions would be strengthened by additional control experiments, especially for the data obtained using FSEC-TS (Fig. 2C) and single fibre recordings (Fig. 3). For instance, how specific is the T105A mutation in abolishing Cl--dependent conformational changes? Did the authors check how the T105A mutation affects the ability of the LBD to undergo conformational changes in response to (1) L-Gln only and (2) Cl- only? Have the authors tried running these experiments at lower Cl- concentrations? 304 mM Cl- (page 16, line 363) is much higher compared to the effective concentration range claimed by the authors. For the single fibre recordings, have the authors tried applying 10 mM NMDG-gluconate? Having this negative control will provide more confidence in the specificity of Cl--induced impulses. Also, we would recommend a demonstration of reversibility in the gurmarin effect shown in Fig 3A.

Additional suggestions for the authors to consider:

1) The introduction would benefit from greater focus and clarity to make the work more accessible to readers. Despite the overall focus on T1rs, only a quarter of the introduction revolves around these receptors. Additional information would help the reader to understand the research topic. For example, how many isoforms are there? Are these receptors obligate heterodimers? How similar are the mf T1r2a/3 compared to the human T1r2/3 receptors? If mf T1r2a/3 receptors are activated by amino acids, how useful a proxy are they in understanding sweet-sensing human T1r2/3 receptors? If T1r3 is found in both heterodimers, and amino acids bind to T1r3, how do these receptors discern between sweet and umami taste? What are the mechanisms underlying activation of these receptors? How are these receptors usually studied functionally?

2) Given the focus on isolated LBDs of (non-human) mfT1r2a/3 receptors, the authors are encouraged to comment on the probability of Cl- binding, and the subsequent conformational rearrangement observed in the isolated LBDs, actually translating to activation of (full-length) human receptors (and ultimately taste stimulation). Since the authors have previously assessed the function of hsT1r2/3 in HEK293 cells using Ca2+ imaging (PMID: 25029362), evaluation of the activation properties of Cl- at full-length receptors and testing the effects of T1r3 mutations on these Cl- effects would help to strengthen the manuscript. Also, there are several reported polymorphisms in the gnomAD database around the Cl- ion binding site (Thr102Met, Gly143Arg, Pro144Ser/Leu), so it would be interesting and helpful to test the effects of these variants that are found in the population. We do not expect the authors to perform these experiments, but in the absence of more conclusive functional data on full-length receptors, the authors should consider discussing these potential caveats in the text.

3) Given the availability of AlphaFold Multimer and the well-defined stoichiometry of the complex, did the authors attempt to predict a model of the full-length heterodimer? This may be informative with regards to the mechanism of signal transduction to the transmembrane domain.

4) The nerve recording data would be more convincing if the authors could provide electrical recordings to truly sweet compounds at physiologically relevant concentrations (sucrose and artificial sweeteners). Currently, they only show data for 20 mM L-glutamine, which is not particularly sweet in Fig 3a-b, and then summary data for sucrose in Fig 3b.

5) The authors may wish to include a comment about whether bromide has the same effect on taste perception as chloride, and point out that gurmarin is a non-selective antagonist. Ideally, the nerve recordings should be done in T1r knockout mice to formally prove the mechanism. Although this may be beyond the scope of this work, a brief mention of this caveat seems warranted.

6) Finally, the discussion would benefit from additional mention of ligand binding in relevant heterodimeric class C GPCRs, as well as the observation that chloride appears to work via a distinct mechanism despite its binding site being spatially very close to that of Gln.

REVIEWING TEAM

Reviewed by:

Alexander T. Chesler, Principal Scientist, NCCIH, NIH, USA: Ion channel function, regulation and physiology

Han Chow Chua, Assistant Professor, University of Copenhagen, Denmark: Ion channel structure and function

Oliver B. Clarke, Assistant Professor, Columbia University, USA: Protein structural biology

Curated by:

Stephan A. Pless, Professor, University of Copenhagen, Denmark

(This consolidated report is a result of peer review conducted by Biophysics Colab on version 1 of this preprint. Minor corrections and presentational issues have been omitted for brevity.)

Biophysics Colab

Consolidated peer review report (13 December 2021)

GENERAL ASSESSMENT

The plasma membrane biogenic amine transporters fulfill important roles in neurotransmission by regulating synaptic serotonin, norepinephrine and dopamine. They are targets for drugs used to treat depression anxiety and other psychiatric disorders and also for drugs of abuse. Additionally, these transporters have been the subject of much research from the 1960’s to the present and have come to represent models for how transporters in general move their substrate neurotransmitters across the plasma membrane and how that process is coupled to transmembrane ion gradients.

This preprint addresses the role of K+ in transport of dopamine (DA) by the Drosophila dopamine transporter (dDAT). In this family, only the serotonin transporter (SERT) had been shown to use the outwardly directed K+ gradient as a driving force for transport. In another transporter family, K+ coupling to transport was shown for excitatory amino acid transporters. The preprint shows interactions between K+ and dDAT in three areas, competition with Na+ for facilitation of inhibitor binding, conformational changes assessed using hydrogen-deuterium exchange and mass spectrometry, and flux studies in proteoliposomes.

Transporters in this family use an inwardly directed Na+ gradient to drive substrate uptake, and two Na+ binding sites have been detected in high resolution structures of these proteins. This preprint presents strong evidence that K+ acts competitively with Na+ to inhibit the ability of dDAT to bind nisoxetine, an inhibitor of the human norepinephrine transporter (hNET) that also binds avidly to dDAT. It also presents some supporting data with hDAT showing similar behavior with another radioligand specific for the human homologue.

The effect of K+ on dDAT conformation was assessed using HDX-MS. Compared with the control condition (200 mM Cs+), dDAT in 200 mM K+ exchanged less D+ for H+ in multiple locations throughout the protein, but found no locations where exchange was enhanced by K+. The measurement was repeated comparing 200 mM Na+ with 200 mM K+. Several of the regions that were stabilized by K+ relative to Cs+ (lower exchange) showed enhanced exchange relative to Na+. Other areas that were stabilized by K+ relative to Na+ were also stabilized relative to Cs+ but several regions that were stabilized relative to Cs+ showed similar exchange rates in Na+ and K+. These results could indicate that K+ induces a more inward-open conformation of dDAT relative to Na+.

The experiments with dDAT reconstituted in proteoliposomes provide the strongest support for the antiport of K+ for dopamine. Successful reconstitution of a biogenic amine transporter has not been convincingly demonstrated and this result represents an important step forward for the field. The data in Fig. 3b and extended data 4a show specific thermodynamic coupling between transmembrane K+ and dopamine gradients. There is some ambiguity in the interpretation of these experiments that will be addressed in the recommendations.

The single vesicle experiments described in Fig. 4 provide additional analysis of Na+ influx and K+ efflux in response to imposition of gradients and addition of substrate. These experiments show in more detail the ion fluxes across the membranes of individual proteoliposomes. In agreement with former measurements of DAT-mediated uncoupled ion fluxes, they show that dDAT catalyzes Na+ influx and K+ efflux even in the absence of dopamine. Fluxes were blocked by nortriptyline, demonstrating that these were catalyzed by dDAT and not due to leaky liposomes.

RECOMMENDATIONS

Revisions essential for endorsement:

There are six changes in the text that we feel are necessary, and only one experiment, which we feel would not be difficult for the authors to perform.

Discussion and calculations:

1. Because the demonstration of coupling between a K+ gradient and DA accumulation is so significant, it is important to show that it represents catalysis – that is, each reconstituted dDAT molecule is capable of transporting multiple molecules of substrate. The figures show only relative amounts (% of maximum, cpm) and no measure of the amount of reconstituted dDAT in the transport assays. Molar ratios of accumulated dopamine and the amount of reconstituted dDAT (which must be known by the authors) can be translated into the number of molecules transported per transporter. The amount of dDAT could be corrected using the data in extended Fig. 4b, to count only functional transporters. Ideally, the DA/dDAT ratio would be much larger than one, to distinguish the uptake from any kind of 1:1 binding phenomenon.
2. There is an alternative explanation for the ability of a K+ gradient to drive DA accumulation in Fig. 3b. Imposing an outwardly directed K+ gradient under conditions where there is K+ efflux would generate a diffusion potential (negative inside) which itself could act as a driving force for DAT if the transport process involves inward movement of positive charge. The coupling between the K+ gradient and DA accumulation could therefore be direct, as it is in SERT, or indirect, mediated by the diffusion potential. Unless the authors have convincing reasons to exclude the possibility the latter possibility, they should include that interpretation as an alternative explanation of the results that cannot be ruled out.
3. The dopamine-independent Na+ and K+ leaks suggest that ion gradients imposed by dilution may not be constant with time. Typically, when ion gradients dissipate with time, substrate transport does not show the stable accumulation observed in Fig. 3b and extended data 4a, but rather an overshoot where a rising phase of accumulation is followed by a falling phase as the driving force of the ion gradients wanes. The relatively rapid increase in intravesicular Na+ and loss of intravesicular K+ shown in Fig. 4b seem in conflict with the long period of stable dopamine accumulation in Fig. 3b. How do the authors explain this difference? The reviewers suggest an experiment in the following section to address this issue.
4. In describing the HDX-MS studies, there should be some explanation for why Cs+ was used as an inert cation while NMDG+ was used for the binding experiments. In addition, the statement that K+ “stabilizes dDAT structural dynamics” is not quite accurate. HDX data suggest that while this is true when compared to Cs+, comparison with Na+ reveals mixed effects on deuterium uptake in presence of K+. The authors have previously shown that there are multiple regions of dDAT displaying EX1 kinetics in presence of Na+ (ref 20). Does this still hold true for K+? Discussion of deuterium uptake kinetics (especially in the areas shown to have displayed on EX2 behavior) would be valuable when comparing the effect of Na+ and K+ on dDAT conformational dynamics. Is there a way the changes in HDX could be explained that would provide some connection with the other observations? For example, could it be argued that the replacement of Na+ with K+ reversed the effect of Na+ at the Na2 site, which is to favor an outward-facing conformation? The statement at the end of the HDX-MS results seems somewhat tepid (“could suggest that K+ induces a more inward facing dDAT state than Na+.”). It would be more helpful for the reader to point out how the HDX-MS results can be interpreted as evidence for a given conformation, perhaps by comparing these results with conformational results obtained by other methods under similar ionic conditions.
5. The preprint presents 4 phenomena connecting K+ to dDAT function. There is competition between K+ and Na+ for inhibitor binding, differences between the effects of Na+ and K+ in HDX studies, the ability of Na+ gradients (and amplification by internal K+) to drive dopamine accumulation, and the ability of dDAT to catalyze K+ and Na+ fluxes across the membrane. What is the connection between the flux studies and the other results? If the authors have any hypotheses that link either of these with the accumulation and ion flux data, they should express them. Otherwise, the binding and HDX-MS data seem unconnected from the rest of the experiments in the study.
6. Another laboratory has published a paper on the role of K+ in dopamine, norepinephrine and serotonin transport (DOI: https://doi.org/10.7554/eLife.67996). That paper concluded that intracellular K+ interacted with each of these transporters but was antiported for substrate only in SERT, not in NET or DAT. This paper was not cited, perhaps by oversight, but it is very relevant, and the authors should address the differences in their conclusions and possibly attempt to explain them.

Experimental work:

1. Additional evidence that ion gradients are driving accumulation of intravesicular dopamine could be obtained easily by dissipating the ion gradients after accumulation using an ionophore such as nigericin, monensin or gramicidin, any of which will exchange Na+ and K+ across the membrane and remove the energetic driving force responsible for dopamine accumulation. If added, for example, at 10 min into the time course of Fig. 3b, any of these would cause rapid efflux of accumulated dopamine if the ion gradients were maintaining dopamine accumulation.

Additional suggestions for the authors to consider:

Discussion:

1. The preprint only briefly addresses the many ways that the proteoliposome preparation could be heterogeneous. Transporters could be inserted in inside-out or right-side-out orientations, some of the dDAT added to the reconstitution process could be inactive, vesicles could have 0, 1, 2… etc. copies of DAT. Some of the results indicate that the number of vesicles that show changes could be affected by dopamine, others show that the rate of change was affected. The authors might want to expand the very brief mention of heterogeneity on the first page of the discussion (page 7) to include these other issues and how they might influence the results.
2. Extended Data Figure 6a shows slow uptake of dopamine in the absence of internal potassium, but the plateau level is the same as in its presence. This would suggest a kinetic effect rather than a thermodynamic effect. On the other hand, this is not observed in Figure 3b. Please explain.
3. It might be useful to know the sequence identity and similarity between dDAT and hDAT.
4. In Extended Data Figure 4a it looks like the counts observed with internal sodium represent uncorrected non-specific binding. Correct?

Experimental:

1. As stated above, the mechanism by which K+ stimulates DA accumulation could be direct antiport or it could be through generation of a membrane potential. One way to address this issue would be to dissipate any potential by adding a proton ionophore such as FCCP or 2,4-dinitrophenol with a pH buffer in both the medium and the proteoliposomes lumen. If the protonophore inhibited DA accumulation, it would suggest that the potential was the driving force and not direct coupling to K+ as the preprint infers.
2. In SERT, a pH difference (acid inside) stimulated 5-HT accumulation in the absence of K+, suggesting that protons could replace K+ ions. That would be interesting to test in this system.
3. One way to show that the ion fluxes in proteoliposomes were catalyzed by dDAT and not a property of the membrane would be to drive ion flux using a H+ diffusion potential. Imposing a pH difference (alkaline inside) in the presence of a proton ionophore should stimulate outward K+ flux. Adding nortriptyline should eliminate the contribution of dDAT to this flux.
4. It would be informative to know if Cl- was required for the processes studied here, which would strengthen the argument that transport by dDAT was involved. For example, it would be interesting to know if Cl- was required for DA-stimulated K+ efflux and Na+ influx, and the accumulation of DA in response to internal K+.

REVIEWING TEAM

Reviewed by:

Suraj Adhikary, Scientist, Janssen Pharmaceuticals, USA: Membrane protein structural biology and biophysics.

Baruch Kanner, Professor, The Hebrew University of Jerusalem, Israel: The molecular mechanism of sodium-coupled neurotransmitter transport.

Christopher Mulligan, Lecturer, University of Kent, UK: Molecular mechanisms of secondary-active transporters.

Gary Rudnick, Professor, Yale University School of Medicine, USA: Mechanisms of membrane transport proteins.

Curated by:

Gary Rudnick, Professor, Yale University School of Medicine, USA

(This consolidated report is a result of peer review conducted by Biophysics Colab on version 1 of this preprint. Minor corrections and presentational issues have been omitted for brevity.)

Biophysics Colab

Authors' response (16 December 2021)

GENERAL ASSESSMENT

The TMEM16 family of membrane proteins have been shown to function as calcium-activated chloride channels and lipid scramblases. In recent years, X-ray and cryo-EM structures have been solved for TMEM16 proteins in ligand-free and ligand-bound conformations, providing valuable structural information on their functional duality and activation mechanisms. It is largely accepted that the catalytic site (termed subunit groove or cavity) is mostly shielded from the membrane in the ligand-free TMEM16 scramblases. Calcium binding induces a conformational rearrangement of the cavity-lining helices, opening the groove to the surrounding membrane. Since the groove is hydrophilic, it was proposed that it serves as a permeation pathway for lipid headgroups while the hydrophobic lipid tails remain embedded into the hydrophobic membrane core, which has been termed the "credit card" mechanism of lipid scrambling. Additionally, structures of several TMEM16 homologs in lipid nanodiscs revealed that these proteins deform the lipid bilayer in the vicinity of the subunit cavity by bending and thinning the membrane, irrespective of the presence of the activating ligand calcium. Functional experiments also suggested that lipids can be scrambled outside of the open subunit cavity and that local protein-induced membrane deformation is critical for lipid scrambling.

In the present study, Falzone and colleagues further address the mechanisms of lipid scrambling using single particle cryo-EM and liposome-based functional assays. Firstly, the authors solved the structure of a calcium-bound fungal homolog, afTMEM16, in nanodiscs with a lipid composition where the protein is maximally active. Although similar structures were obtained before, this new structure has the highest resolution thus far, representing \> 1 Å improvement! The structure is beautiful and is a major achievement, which enabled the authors to resolve individual lipids and their interaction with the protein around the subunit cavity, whereas in previous structures unresolved non-protein densities were observed passing through the groove. The authors also solved a number of structures with and without calcium in lipid compositions that promote (thinner lipid bilayers) or suppress (thicker lipid bilayers) scrambling. The authors show that afTMEM16 can scramble lipids while the subunit groove remains closed, a phenomenon that is further enhanced in thinner membranes, whereas in thicker membranes scrambling is suppressed even though the groove is open. We particularly appreciated how different software packages and processing strategies were used to rigorously identify structural heterogeneity in their cryo-EM data. Remarkably, mutations of residues lining the subunit cavity and interacting with lipids do not appear to have dramatic effects on scrambling rates, which suggests that lipids do not need to interact with the protein to be scrambled. Thus, the overall conclusion of the study is that membrane thinning by TMEM16 scramblases in their calcium-free conformation is enough to induce lipid scrambling, and that the groove opening induced by calcium binding further enhances membrane deformation, promoting faster scrambling. By contrast, in thicker membranes the protein fails to sufficiently deform the bilayer and scrambling is suppressed, even when the subunit groove is open. The present study provides unprecedented structural information on the interaction of lipids with afTMEM16 and new evidence that lipids can be scrambled outside of the groove.

The findings and conclusions presented here help to explain why TMEM16 scramblases can transport lipids with headgroups much bigger than the dimensions of the subunit cavity and why structures of some of the other scramblases (opsins, Xkrs and mammalian homolog TMEM16F) lack the obvious hydrophilic groove seen in fungal TMEM16 scramblases. Overall, this is a well-rounded study with an exceptional amount of high-quality cryo-EM data and functional experiments supporting the conclusions.

We thank the reviewers for their praise of our work and for their constructive criticisms. Below we provide a detailed response to their comments and suggestions.

RECOMMENDATIONS

Revisions essential for endorsement:

1) The resolved lipids binding within the groove in the first structure might be seen by some as supporting the credit card mechanism as it definitively demonstrates that lipids reside within the groove. While the authors provide evidence that lipids can permeate outside the groove in this and earlier work, as far as we can tell, none of that would preclude permeation through the groove if it doesn't require specific interactions between lipids and sidechains in the protein. The presentation might be improved with a somewhat more circumspect and nuanced exposition of the new data and how it can be understood with earlier results.

There are several reasons why we do not think that the lipids in the C18/Ca2+ structure support the credit card mechanism, at least in the incarnation proposed for the TMEM16 scramblases.

1. In the credit card model, lipid headgroups enter and traverse the whole span of the groove (as described in multiple publications, i.e. Bethel and Grabe, PNAS, 2016; Jiang et al., Elife, 2018; Lee et al., Nat Comms, 2018; Kostriskii and Machtens, Nat Comms, 2021). The lipid densities near the groove suggest that P3 and P4 lipids are oriented with their heads facing the groove's exterior, not the interior. These heads are contiguous with other resolved lipids in the outer and inner leaflets, respectively. We added panels showing views of the pathway from the extracellular solution to better convey that the lipid heads do not enter the groove (see new Fig. 1F-G). We also added a statement on pg. 10 to clarify this important point.
2. In the present structures, which are consistent with earlier ones with lower resolution (Falzone et al., Elife, 2019; Kalienkova et al., Elife, 2019), residues in the extracellular vestibule do not interact with lipids (see new panels 1E-G). In contrast, the wide intracellular vestibule is embedded in the membrane. We agree with the reviewers that lipid headgroups can, and likely will, enter this wide vestibule during scrambling. We modified the text on pg. 12 to clearly state this point "The wide intracellular vestibule is embedded in the nanodisc membrane and, at the open pathway, the resolved P3 and P4 lipids have opposite orientations (Fig. 2A), suggesting scrambling might occur between them. In this case, the lipid headgroups would only need to move through the wide intracellular vestibule of the pathway below the T325-Y432 constriction rather than through the whole groove (Fig. 2A)."

These observations, together with the extensive mutagenesis data reported in Fig. 2 and 3, point to a mechanism that is different from the precisely coordinated credit-card mechanism that is the currently accepted paradigm for lipid scrambling.

Might the complex composition of native lipid membranes influence where and by what mechanism lipid movement between leaflets is catalysed by TMEM16 proteins?

The idea that the lipid composition might affect the mechanism of scrambling (i.e. through the groove vs out of the groove) is very interesting, and we are actively investigating it in the lab. However, it would be surprising if different lipids were scrambled by entirely different mechanisms.

2) The quality of lipid densities in cryo-EM structures is greatly affected by the number of particles used and the resolution obtained during refinement and it is therefore not surprising that the beautiful lipid densities observed here in the structure of afTMEM16 in lipid nanodiscs in the presence of calcium refined to 2.3 Å are not all observed in subsequent structures with lower resolution. This is true not only for the P lipids near the groove, but for those D lipids bound near the dimer interface, which is a stable region of the protein that does not change conformation. To be cautious, the authors should avoid resting any conclusions on the absence of lipid densities in the lower resolution structures. For example, on pg 15 the authors seem to be interpreting the absence of density for C22 lipids.

We agree with the reviewers on this point. However, at ~2.7 Å average resolution and with \>130,000 particles we would expect to see density for lipids near the pathway, if these were tightly bound. For example, in the mTMEM16F nanodisc structures from the Chen and Jan labs (Feng et al., Cell Reports, 2020), several lipid densities were identified near the closed pathway despite a substantially lower average resolution. However, we agree that we should not interpret this lack of signal and toned down our statement, "This suggests that the interactions of C22 lipids with the pathway helices are weaker than those of C18 lipids, possibly reflecting a higher energy cost associated with distorting these longer acyl chain lipids" to better indicate this is a possible explanation, rather than a definitive mechanistic interpretation.

3) The presentation of structural interactions between lipids and residues near the groove of the protein could be improved in the figures. A panel like Fig. 1J but for the groove would help, but it would be good to see expanded perspectives in the form of a supplementary figure where residues around the headgroup of the lipids are shown along with EM maps so the quality of the structural information for both lipids and side chains can be better appreciated. The preprint does have a lot of images of the lipids and the protein, but not in a way that enables the reader to quickly grasp the nature of interactions between side chains and lipid moieties for themselves, and we feel that close-ups of individual lipids as suggested above would help.

We thank the reviewers for this suggestion. We show density maps for the protein and lipids in Fig. 1C-E, and added close-up views of the densities near the groove in the new Fig. 1F-G to highlight the poses adopted by the lipids in this region. Figures showing both density and atomic models for the protein and lipids are very busy and difficult to discern; many of the lipids interact with multiple residues from different helices, with both their heads and tails. As such we could not find satisfactory views displaying both for the majority of the lipids.

It is also not clear what the authors mean by "lipid headgroup". Have the authors only considered interactions of the phospholipid phosphate group with protein residues? It would be helpful if the authors could clarify this in the manuscript and say whether other types of interactions were considered.

In our C18/Ca2+ map, we resolve a total of 16 lipids per monomer. Of these, we assigned 2 as PG lipids, because we could resolve the large PG headgroup (D4 and D5), shown in Fig. 1F-H and Supp. Fig 2. In all other cases, we truncated the lipids at the phosphate, as the density was insufficient to distinguish between a PC and a PG headgroup. This is now specified in the Fig. 1 legend. In our mutagenesis experiments (Fig. 2 and 3), we only targeted residues that were within interaction distance of the resolved portions of the headgroups, which is the phosphate in most cases. This is now clarified on page 11 "we investigated how mutating residues coordinating the resolved portions of the headgroups of P1-2 and P4-6 impacts scrambling."

It would also be nice to include a close-up view of D511A/E514A in 0.5 mM calcium with cryo-EM density to demonstrate the absence of bound calcium ions.

We thank the reviewers for this suggestion. We added a new panel in Supp. Fig. 10H showing a close-up of the cryoEM density of the mutant binding site.

4) The functional data in Fig 2, 3 and 4 are also not discussed in much detail and it would help if the authors could expand the presentation. Although scrambling in the presence of a very high concentration of calcium is not dramatically altered by any of the mutations, there is quite a lot going on in the absence of calcium and very little is said about these results. For example, differences in the scrambling rates can be observed with some mutants in the presence and absence of calcium in figures 2E and 3E, but statistical analysis would be required to know if the differences between mutants are significant. The differences in scrambling rates with different lipids are also not discussed (e.g. Fig. 4A) It would help if the authors could discuss what is the margin of error in the scrambling assay, and point to some concrete examples from their earlier work on this specific scramblase where mutants have a large impact on scrambling activity in their assay.

We agree with the reviewers that most mutants show some effects in 0 Ca2+. The effects are statistically significant for all but one mutant (2-tailed t-test, p\<0.005). However, the magnitude of the effects is relatively small (\<7-fold reductions in all cases). While our approach to quantify the scrambling rate constant captures well large changes, some of the assumptions underlying the analysis make it less well suited to quantify small effects. In past publications we used a 10-fold change as a cut-off threshold to consider an effect meaningful (Lee et al., Nat comms, 2018; Khelashvili, Falzone et al., Nat Comms, 2020). These limitations and rationale for choices are discussed in several of our past publications (Malvezzi et al., PNAS, 2018; Lee et al., Nat Comms, 2018; Falzone and Accardi, MiMB, 2020). We added statements indicating magnitude of the observed reduction for the mutants in the various conditions. We prefer to refrain from presenting statistical significance of these results as we do not want to convey the idea these effects are more meaningful than they might be.

Have the authors tried intermediate more physiologically relevant concentrations of calcium to see if the mutants have discernible effects under those conditions?

This is an excellent suggestion. However, in our experience the technical limitations of the experimental set-up and of the analysis render a precise quantification of small effects at intermediate Ca2+ concentrations not very reliable. For this reason, we did not pursue this further.

5) It is quite intriguing that the mutations in the subunit groove of afTMEM16 have little effect on scrambling activity. The authors propose that the groove-lining residues are not directly involved in lipid coordination even though their structure suggests that they do and there is a wealth of functional studies and MD simulations on various other TMEM16 homologs suggesting otherwise.

We are a bit confused by the reviewers' statement that our structure suggests that groove lining residues coordinate lipids. In our structures, the only two residues that directly line the open groove and coordinate lipids are T325 and Y432 (Fig. 2A). All other 23 residues tested either do not line the groove (9 residues mutated in Fig. 2) or do not interact with lipids (14 residues mutated in Fig. 3). The finding that mutating these residues has minor effects on scrambling suggests that interactions between lipids and these side chains is not required for scrambling.

We agree that the overall lack of effect of the mutants is surprising, especially in light of past work. However, none of the scrambling assays (in vitro or cell-based) can distinguish between mutations that affect permeation from those that affect gating. All that is measured is whether and -to a degree- how well lipids are transported. As such, we propose that at least some of the functional effects could have been misinterpreted. We are currently testing this hypothesis in the lab.

The discrepancy between our structural and functional results and the molecular mechanism emerging from MD simulations is more striking. Although some differences exist between the reports of different groups, the overall agreement among them is excellent. We were thus surprised that our data is so difficult to reconcile with their observations. Indeed, the extensive mutagenesis reported in Fig. 2 and 3 was performed to systematically test the unexpected inferences of our initial structural results (on the C18/Ca2+ structure). Our conclusions are also corroborated by the structures in different lipid compositions. In the discussion (pg. 21-22) we consider some of the possible sources for these discrepancies. For example, while in the MD simulations of nhTMEM16 the extracellular vestibule (i.e. E305, E310 and R425) is immersed in the groove, in our cryoEM maps we do not see evidence of lipids interacting with these residues (Fig. 1,2,3). Notably, a similar arrangement of the membrane-protein interface is seen in the Ca2+-bound open nhTMEM16 structure in nanodiscs (Kalienkova et al., Elife, 2019), indicating this issue is not specific to afTMEM16 or to the nanodisc used. We hypothesize this different membrane-protein interface is at the origin of the different proposed mechanisms. Another potentially relevant difference is that the tails of multiple lipids intercalate between helices forming the dimer cavity, some of which line the groove (Fig. 1). These lipids were not included in MD simulations as they were not previously resolved, and they could affect groove dynamics and, consequently, its interactions with the membrane. Other possibilities exist, but we believe they are less likely to be important (i.e. the limited nature of nanodiscs used for the cryoEM experiments could influence the protein-membrane interface, the mutations could have effects that are too subtle to measure in our assay). However, we think that enumerating all possibilities would lead to an overly lengthy discussion and require too much speculation.

We have revised the discussion of these important points in pg. 21-23 to better convey these uncertainties and added a statement (pg. 11) where we report the distance between the phosphate atom of the P3 lipid and E305 (13.7 Å), E310 (17.9 Å) and R425 (15.7 Å).

The authors' suggestion that mutations probably affect the equilibrium between open and closed conformations of the groove in other homologs but not in afTMEM16 is logical, however, there are some discrepancies. To name a few examples, if indeed this is the case, nhTMEM16 mutants with closed groove should still have significant basal scrambling, by extrapolation from afTMEM16 data. Yet, some of the nhTMEM16 mutants (E313/E318/R432 mutants) have no activity at all, or no basal scrambling activity (Y439A) (Lee et al, 2018). Would you expect that point mutations within the subunit groove remove the ability of the protein to deform the membrane in its closed conformation? Might the groove have intermediate conformations between closed and fully open where the mutants studied might have more impact in afTMEM16?

These are excellent ideas, and we are actively pursuing them in the lab. However, at the moment results are too preliminary to draw firm conclusions.

Further, mutating some of the residues on the scrambling domain of TMEM16 affected externalization of some lipid species, but not internalization etc. (Gyobu et al, 2017), which should not be the case if the interaction of the protein with the lipids is completely unnecessary for lipid scrambling.

This is a good point. However, mechanistic interpretation of results from cell-based scrambling assays is quite tricky, even more so than of the results from the in vitro measurements used in the present work. The presence of other lipid transporters and/or scramblases, or a multitude of other factors, could influence the results. For example, in cells scrambling by TMEM16F is delayed, it takes ~10 minutes after Ca2+ exposure to begin seeing PS externalization. In contrast, in in vitro measurements TMEM16F responds to Ca2+ nearly instantaneously, within the ~1 s mixing time of the cuvette (Alvadia et al., Elife, 2019). Thus, a direct comparison of the results obtained in cells and in vitro is not straightforward. More work is needed to investigate these important points.

While investigating this question further would require follow-up structural studies on other TMEM16 homologs and is outside of the scope of this study, we think that the manuscript would benefit from a more extensive discussion on contradicting results and alternative interpretations. The authors might want to consider the possibility that there may be substantial variations in how different scramblases function.

We agree that it is a priori possible that different TMEM16 proteins function according to different paradigms. However, we think this is an unlikely possibility. Despite differences in their gating behavior, most basic functional properties of TMEM16s are well conserved. Thus, fundamentally different mechanisms (i.e. through the groove or out of the groove) would have to result in similar functional phenotypes. We find the hypothesis that the basic scrambling mechanism is conserved among different TMEM16 homologues more plausible. While our results do not rule out that through the groove scrambling can occur, they suggest that it is not the main mechanism for afTMEM16, despite the fact that this protein adopts a very stable conformation with an open groove. Therefore, we consider the possibility of different mechanisms unlikely. This is mentioned on pg. 22 of the discussion.

afTMEM16 has high constitutive activity in the absence of calcium, while at least TMEM16F does not. Additionally, the extent to which scrambling is promoted by calcium varies, as mammalian scramblases might need other cellular factors to be activated. Also, the extent to which scramblases are seen to distort the membrane is highly variable, as again seen in TMEM16F structures. Might some of these differences imply that key aspects of the mechanism of scrambling (e.g. thinning of the membrane or whether lipids scramble inside or outside the groove) are not the same for all scramblases? This might be one way to organize the discussion to help reconcile some of the seemingly divergent findings in the field.

The reviewers raise an excellent point. Indeed, we find that for all TMEM16 homologues we have tested in the lab the degree of activity in 0 Ca2+ is highly dependent on the lipid composition. However, this does not appear to correlate with changes in conformation, as we report here for afTMEM16 and as reported by other groups for nhTMEM16 and TMEM16F.

6) The authors should correct the Ramachandran outliers in C18/calcium and C22/calcium structures.

We tried fixing the Ramachandran outliers, however this invariably led to worse fits of the atomic models with the density. Therefore, we believe it is appropriate to leave them as they are.

Additional suggestions for the authors to consider:

1) In several instances the authors conceptualize hypothetical mechanisms to set up experiments and frame their interpretations, which is not always the most straightforward way to communicate findings and what they reveal. The 'conveyor belt mechanism' introduced on page 10 is never fully defined in a way that helps the reader to understand what the functional effects of the mutants teach us. Might it be easier to set up the experiment by asking whether the interactions between sidechains that apparently interact with lipid headgroups in the structure play a critical role in scrambling, present the results and then conclude that they do not appear to? Collectively the functional effects of mutants do appear to suggest that specific side chain interactions are not critical for scrambling, but the conceptualized mechanism here makes the conclusions come across as unnecessarily forced.

We thank the reviewers for the suggestion. We agree that the conveyor belt mechanism is a bit of a strawman. However, it is a plausible mechanism based on the orientation of the lipids in the C18/Ca2+ map. The mutagenesis described in Fig. 2 was explicitly designed to test this possibility. Further, this allows us to draw a clear distinction between testing the roles of residues outside the groove and of side chains that directly line the groove.

The credit-card mechanism has been formally introduced and discussed in the field but has already been shot down in earlier work from the group and seems overly simplistic if we already know that scrambling can occur both inside and outside the groove from earlier studies. Just something for the authors to think about.

We do not believe our previous work (Malvezzi et al., PNAS, 2018) 'shot down' the credit-card model. While we proposed that the large, PEG-conjugated lipid headgroups traverse the membrane outside the groove, our model postulated that normal-sized headgroups were scrambled within the groove. Further, one of the recurring criticisms of that work, was that the path taken by the large PEG-conjugated lipids might not represent a physiologically relevant mechanism for normal lipids. Thus, the credit-card mechanism remained the dominant model to explain scrambling, as testified by many subsequent publications by multiple groups, including our own!

2) The uninitiated reader would greatly benefit from more of an introduction to the functional scrambling assay in the results and material and methods section so they can understand the results being presented. In the Material and methods, the authors mentioned: "All conditions were tested side by side with a control preparation", perhaps add here what exactly served as control –wild type protein in C18 lipids? It would be valuable to include information on the reconstitution efficiency between their preparations (WT in different lipid compositions and WT vs mutants). these if possible.

We thank the reviewers for this suggestion. We added a brief description of the assay in the Methods section and now specify that "All conditions were tested side by side with a control preparation of WT afTMEM16 reconstituted in C18 lipids."

3) Also, does the C18/calcium cryo-EM structure have sufficient resolution to distinguish between specific phospholipids (PG or PC) at the D1-D9 or P1-P7 positions? It would be particularly valuable if the authors could comment on whether PG or PC are observed in the D and P positions, or which lipids are lining the groove (P3-P6).

We could build 2 lipids as PG (D4 and D5), based on the presence of density that could accommodate the large PG headgroup. For other lipids, the density was too weak beyond the phosphate, and therefore we left them truncated. This is now stated in the Figure 1 legend.

4) While not essential, it would be interesting if the authors could perform the assay on the mutants with a more prominent effect in the absence of calcium (e.g. E310A, Y319A/F322A/K428A) with several additional calcium concentrations.

We thank the reviewers for this suggestion. However, as we noted above, given the relatively small effects and limitations of the assay, we do not believe we would be able to extract meaningful mechanistic information from these measurements in intermediate conditions.

5) The authors mentioned that the interaction of C22 lipids with the pathway helices is weaker than those of C18 lipids, which reflects the energy cost associated with distorting the longer lipids (page 15). However, they claimed that the interaction between the lipids and residues is not important for scrambling, which seems contradictory.

We apologize for the confusion. In our proposed model, the ability of afTMEM16 to thin the membrane is dictated by the interactions of the protein with the surrounding lipids. This is not only enabled by interactions between side chains and lipid headgroups, but also by interactions of the lipid tails interact with the protein (see for example the close-up panels in Supp. Fig. 2F-G and the text on pg. 11 "Rather, other factors, such as tail interactions with interhelical grooves, contribute to their association with afTMEM16 (Supp. Fig 2F-G) and stabilize the distorted membrane-protein interface that results in thinning at the pathway.")

(This is a response to peer review conducted by Biophysics Colab on version 1 of this preprint.)

Biophysics Colab

Consolidated peer review report (30 November 2021)

GENERAL ASSESSMENT

The TMEM16 family of membrane proteins have been shown to function as calcium-activated chloride channels and lipid scramblases. In recent years, X-ray and cryo-EM structures have been solved for TMEM16 proteins in ligand-free and ligand-bound conformations, providing valuable structural information on their functional duality and activation mechanisms. It is largely accepted that the catalytic site (termed subunit groove or cavity) is mostly shielded from the membrane in the ligand-free TMEM16 scramblases. Calcium binding induces a conformational rearrangement of the cavity-lining helices, opening the groove to the surrounding membrane. Since the groove is hydrophilic, it was proposed that it serves as a permeation pathway for lipid headgroups while the hydrophobic lipid tails remain embedded into the hydrophobic membrane core, which has been termed the "credit card" mechanism of lipid scrambling. Additionally, structures of several TMEM16 homologs in lipid nanodiscs revealed that these proteins deform the lipid bilayer in the vicinity of the subunit cavity by bending and thinning the membrane, irrespective of the presence of the activating ligand calcium. Functional experiments also suggested that lipids can be scrambled outside of the open subunit cavity and that local protein-induced membrane deformation is critical for lipid scrambling.

In the present study, Falzone and colleagues further address the mechanisms of lipid scrambling using single particle cryo-EM and liposome-based functional assays. Firstly, the authors solved the structure of a calcium-bound fungal homolog, afTMEM16, in nanodiscs with a lipid composition where the protein is maximally active. Although similar structures were obtained before, this new structure has the highest resolution thus far, representing > 1 Å improvement! The structure is beautiful and is a major achievement, which enabled the authors to resolve individual lipids and their interaction with the protein around the subunit cavity, whereas in previous structures unresolved non-protein densities were observed passing through the groove. The authors also solved a number of structures with and without calcium in lipid compositions that promote (thinner lipid bilayers) or suppress (thicker lipid bilayers) scrambling. The authors show that afTMEM16 can scramble lipids while the subunit groove remains closed, a phenomenon that is further enhanced in thinner membranes, whereas in thicker membranes scrambling is suppressed even though the groove is open. We particularly appreciated how different software packages and processing strategies were used to rigorously identify structural heterogeneity in their cryo-EM data. Remarkably, mutations of residues lining the subunit cavity and interacting with lipids do not appear to have dramatic effects on scrambling rates, which suggests that lipids do not need to interact with the protein to be scrambled. Thus, the overall conclusion of the study is that membrane thinning by TMEM16 scramblases in their calcium-free conformation is enough to induce lipid scrambling, and that the groove opening induced by calcium binding further enhances membrane deformation, promoting faster scrambling. By contrast, in thicker membranes the protein fails to sufficiently deform the bilayer and scrambling is suppressed, even when the subunit groove is open. The present study provides unprecedented structural information on the interaction of lipids with afTMEM16 and new evidence that lipids can be scrambled outside of the groove.

The findings and conclusions presented here help to explain why TMEM16 scramblases can transport lipids with headgroups much bigger than the dimensions of the subunit cavity and why structures of some of the other scramblases (opsins, Xkrs and mammalian homolog TMEM16F) lack the obvious hydrophilic groove seen in fungal TMEM16 scramblases. Overall, this is a well-rounded study with an exceptional amount of high-quality cryo-EM data and functional experiments supporting the conclusions.

RECOMMENDATIONS

Revisions essential for endorsement:

1) The resolved lipids binding within the groove in the first structure might be seen by some as supporting the credit card mechanism as it definitively demonstrates that lipids reside within the groove. While the authors provide evidence that lipids can permeate outside the groove in this and earlier work, as far as we can tell, none of that would preclude permeation through the groove if it doesn't require specific interactions between lipids and sidechains in the protein. The presentation might be improved with a somewhat more circumspect and nuanced exposition of the new data and how it can be understood with earlier results. Might the complex composition of native lipid membranes influence where and by what mechanism lipid movement between leaflets is catalysed by TMEM16 proteins?

2) The quality of lipid densities in cryo-EM structures is greatly affected by the number of particles used and the resolution obtained during refinement and it is therefore not surprising that the beautiful lipid densities observed here in the structure of afTMEM16 in lipid nanodiscs in the presence of calcium refined to 2.3 Å are not all observed in subsequent structures with lower resolution. This is true not only for the P lipids near the groove, but for those D lipids bound near the dimer interface, which is a stable region of the protein that does not change conformation. To be cautious, the authors should avoid resting any conclusions on the absence of lipid densities in the lower resolution structures. For example, on pg 15 the authors seem to be interpreting the absence of density for C22 lipids.

3) The presentation of structural interactions between lipids and residues near the groove of the protein could be improved in the figures. A panel like Fig. 1J but for the groove would help, but it would be good to see expanded perspectives in the form of a supplementary figure where residues around the headgroup of the lipids are shown along with EM maps so the quality of the structural information for both lipids and side chains can be better appreciated. The preprint does have a lot of images of the lipids and the protein, but not in a way that enables the reader to quickly grasp the nature of interactions between side chains and lipid moieties for themselves, and we feel that close-ups of individual lipids as suggested above would help. It is also not clear what the authors mean by "lipid headgroup". Have the authors only considered interactions of the phospholipid phosphate group with protein residues? It would be helpful if the authors could clarify this in the manuscript and say whether other types of interactions were considered. It would also be nice to include a close-up view of D511A/E514A in 0.5 mM calcium with cryo-EM density to demonstrate the absence of bound calcium ions.

4) The functional data in Fig 2, 3 and 4 are also not discussed in much detail and it would help if the authors could expand the presentation. Although scrambling in the presence of a very high concentration of calcium is not dramatically altered by any of the mutations, there is quite a lot going on in the absence of calcium and very little is said about these results. For example, differences in the scrambling rates can be observed with some mutants in the presence and absence of calcium in figures 2E and 3E, but statistical analysis would be required to know if the differences between mutants are significant. The differences in scrambling rates with different lipids are also not discussed (e.g. Fig. 4A) It would help if the authors could discuss what is the margin of error in the scrambling assay, and point to some concrete examples from their earlier work on this specific scramblase where mutants have a large impact on scrambling activity in their assay. Have the authors tried intermediate more physiologically relevant concentrations of calcium to see if the mutants have discernible effects under those conditions?

5) It is quite intriguing that the mutations in the subunit groove of afTMEM16 have little effect on scrambling activity. The authors propose that the groove-lining residues are not directly involved in lipid coordination even though their structure suggests that they do and there is a wealth of functional studies and MD simulations on various other TMEM16 homologs suggesting otherwise. The authors' suggestion that mutations probably affect the equilibrium between open and closed conformations of the groove in other homologs but not in afTMEM16 is logical, however, there are some discrepancies. To name a few examples, if indeed this is the case, nhTMEM16 mutants with closed groove should still have significant basal scrambling, by extrapolation from afTMEM16 data. Yet, some of the nhTMEM16 mutants (E313/E318/R432 mutants) have no activity at all, or no basal scrambling activity (Y439A) (Lee et al, 2018). Would you expect that point mutations within the subunit groove remove the ability of the protein to deform the membrane in its closed conformation? Might the groove have intermediate conformations between closed and fully open where the mutants studied might have more impact in afTMEM16? Further, mutating some of the residues on the scrambling domain of TMEM16 affected externalization of some lipid species, but not internalization etc. (Gyobu et al, 2017), which should not be the case if the interaction of the protein with the lipids is completely unnecessary for lipid scrambling. While investigating this question further would require follow-up structural studies on other TMEM16 homologs and is outside of the scope of this study, we think that the manuscript would benefit from a more extensive discussion on contradicting results and alternative interpretations. The authors might want to consider the possibility that there may be substantial variations in how different scramblases function. afTMEM16 has high constitutive activity in the absence of calcium, while at least TMEM16F does not. Additionally, the extent to which scrambling is promoted by calcium varies, as mammalian scramblases might need other cellular factors to be activated. Also, the extent to which scramblases are seen to distort the membrane is highly variable, as again seen in TMEM16F structures. Might some of these differences imply that key aspects of the mechanism of scrambling (e.g. thinning of the membrane or whether lipids scramble inside or outside the groove) are not the same for all scramblases? This might be one way to organize the discussion to help reconcile some of the seemingly divergent findings in the field.

6) The authors should correct the Ramachandran outliers in C18/calcium and C22/calcium structures.

Additional suggestions for the authors to consider:

1) In several instances the authors conceptualize hypothetical mechanisms to set up experiments and frame their interpretations, which is not always the most straightforward way to communicate findings and what they reveal. The 'conveyor belt mechanism' introduced on page 10 is never fully defined in a way that helps the reader to understand what the functional effects of the mutants teach us. Might it be easier to set up the experiment by asking whether the interactions between sidechains that apparently interact with lipid headgroups in the structure play a critical role in scrambling, present the results and then conclude that they do not appear to? Collectively the functional effects of mutants do appear to suggest that specific side chain interactions are not critical for scrambling, but the conceptualized mechanism here makes the conclusions come across as unnecessarily forced. The credit-card mechanism has been formally introduced and discussed in the field but has already been shot down in earlier work from the group and seems overly simplistic if we already know that scrambling can occur both inside and outside the groove from earlier studies. Just something for the authors to think about.

2) The uninitiated reader would greatly benefit from more of an introduction to the functional scrambling assay in the results and material and methods section so they can understand the results being presented. In the Material and methods, the authors mentioned: "All conditions were tested side by side with a control preparation", perhaps add here what exactly served as control – wild type protein in C18 lipids? It would be valuable to include information on the reconstitution efficiency between their preparations (WT in different lipid compositions and WT vs mutants). these if possible.

3) Also, does the C18/calcium cryo-EM structure have sufficient resolution to distinguish between specific phospholipids (PG or PC) at the D1-D9 or P1-P7 positions? It would be particularly valuable if the authors could comment on whether PG or PC are observed in the D and P positions, or which lipids are lining the groove (P3-P6).

4) While not essential, it would be interesting if the authors could perform the assay on the mutants with a more prominent effect in the absence of calcium (e.g. E310A, Y319A/F322A/K428A) with several additional calcium concentrations.

5) The authors mentioned that the interaction of C22 lipids with the pathway helices is weaker than those of C18 lipids, which reflects the energy cost associated with distorting the longer lipids (page 15). However, they claimed that the interaction between the lipids and residues is not important for scrambling, which seems contradictory.

REVIEWING TEAM

Reviewed by:

Angela Ballesteros, Research Fellow (K.J. Swartz lab, NINDS, USA): structural biology (X-ray crystallography), membrane protein function, lipid scrambling, cell biology, fluorescence microscopy

Valeria Kalienkova, Postdoctoral Fellow (C. Paulino lab, University of Groningen, The Netherlands): membrane structural biology (X-ray crystallography and cryo-EM), membrane transport and lipid scrambling

Kenton J. Swartz, Senior Investigator, NINDS, USA: ion channel structure and mechanisms, chemical biology and biophysics, electrophysiology and fluorescence spectroscopy

Curated by:

Kenton J. Swartz, Senior Investigator, NINDS, USA

(This consolidated report is a result of peer review conducted by Biophysics Colab on version 1 of this preprint. Minor corrections and presentational issues have been omitted for brevity.)

Consolidated peer review report (18 September 2021)

GENERAL ASSESSMENT

Lipids are known to modulate the activity of many different ion channels, with different functional outcomes depending on type of lipid, ion channel subtype, and site and mechanism of action. Thus, lipids are important endogenous modulators of channel activity and cellular physiology, and have inspired development of pharmacological compounds that mimic lipid effects. However, the effect of lipids on several members of the extensive family of K2P channels, involved in regulating cellular excitability and hormone secretion, as examples, remains relatively unstudied. The work by Riel and co-workers addresses this by studying the effect of the polyanionic lipids PIP2 and Oleoyl-CoA on 12 mammalian K2P channels expressed in Xenopus oocytes, using electrophysiology. The systematic comparison of the lipid response of different K2P subtypes allows the authors to identify which K2P subtypes that respond to PIP2 and Oleoyl-CoA and whether the lipids activate or inhibit channel activity. Interestingly, members of the TREK, TALK and THIK subfamilies are in general activated by polyanionic lipids. In contrast, members of the TASK, TWIK and TRESK subfamilies are in general inhibited by polyanionic lipids or insensitive. Moreover, the authors explore properties of the lipid and some K2P channel subtypes important for the effect, which provides indications of putative underlying mechanisms of action. The authors conclude that many members of the K2P family of ion channels are highly sensitive to polyanionic lipids, with versatile responses depending on channel subtype, and suggest that PIP2-induced inhibition of specific TASK channels is mediated through a newly identified gate in the ion-permeation pathway.

The manuscript is clearly presented and offers a comprehensive view of how channels in the K2P family respond to PIP2 and LC-CoAs. The findings of the present study are of interest to the field and are likely to be of physiological importance. A strength of the work is the systematic comparison of the responses of a large set of K2P subtypes under similar experimental conditions, which allows the authors to draw conclusions about subtype specific responses without the caveat of comparing data collected in different experimental models and by different research groups. However, specific aspects of how experiments and analysis were performed, and the basis for how mechanistic conclusions were drawn could be better described. In the future, it will be interesting to carry out additional mechanistic studies to localize the binding sites for these lipids and to explore the physiological relevance of lipid modulation.

RECOMMENDATIONS

Revisions essential for endorsement:

1. It is interesting that the authors address the putative mechanistic basis for PIP2 and LC-CoA effects. However, this discussion should be extended by more clearly explaining how the authors envision the so-called X-gate to be involved in lipid effects. Do the authors believe that the L244 and R245 residues are directly involved in PIP2 binding/effects or is a downstream functional X-gate required for lipid effects in another site? Similarly, the authors should develop their hypothesis about the role of the SF-gate in lipid effects. Could these polyanionic lipids flip-flop to the extracellular leaflet of the membrane to interact with the SF-gate directly or indirectly, or are these effects likely to be mediated from the intracellular leaflet (as indicated in Figure 5)? Are there any indication of lipid effects when applied in the extracellular solution?
2. We appreciate that the authors present their data as a condensed results text. However, the manuscript would benefit from a more extensive description of how specific experiments and analysis were performed, to facilitate for readers outside the K2P field. One of the important conclusions of this study is that different K2P subtypes respond differently to polyanionic lipids. To further consolidate this conclusion, the authors could more extensively describe how they control that effects are truly mediated by the lipid. In particular, the authors could describe how they handle experiments with current run-down under control conditions (such as examples in Figure 1D and Figure 2B for TWIK-1), as current run-down under control conditions could mask activating effects or exaggerate inhibiting effect. Moreover, the authors show some examples of control experiments with vehicle only (DMSO, like in Supplementary Figure S1I). However, it is not clear to us if control experiments with vehicle were performed systematically for all channels or if DMSO was always added to the control solution. Also, it is unclear what final concentrations of DMSO in the perfusate were achieved in the electrophysiology experiments. Please clarify these points and comment on whether any of the channels are sensitive to DMSO per se, which could complicate quantification of lipid effects. Lastly, what was the rationale behind quantifying effects at +80 mV for the data shown in Figure 3 (but at +40 mV for other data sets)? Why was RbCl, instead of KCl, used in some experiments and why was the lipid effect in those cases relative the Rb+ effect instead of the basal effect? Also, please explain the rationale of using TPA, which is listed in the methods section and used in Figure 4. Do we assume correctly that TPA is used to quantify the "unblockable current" described in the concentration-response quantification?
3. The authors should include statistical analysis throughout their manuscript.

Additional suggestions for the authors to consider:

1. Abstract: Given there are K2P channels tested that do not show significant response to PIP2 (TWIK1, TRESK) or LC-CoA (TASK-1), the statement "we report strong effects of polyanionic lipids for all tested K2P channels" should be revised.
2. Methods: A known activating mutation in hTHIK-2 is introduced to increase surface expression and macroscopic currents. It is not clear whether this activating mutation affects phospholipids response.
3. The fact that TASK-2 belongs to the TALK, and not TASK, family may be confusing to readers outside the K2P field. Especially since TASK-2 shows a lipid response more similar to that of TASK-1 and TASK-3 than that of TALKs. To avoid confusion, the authors could make a note in the introduction (following the sentence "Members of the TALK subfamily are activated by high pH") to point out that despite the name, TASK-2 belongs to the TALK family.
4. The results section under sub-heading "PIP2 causes subtype-dependent responses (activation/inhibition) in most K2P channel" is not easy to follow. This is mainly because the authors do not describe the results in the order the panels in Figure 1 are presented. We suggest that the authors revise the text or the figure to harmonize the order of data presentation.
5. Page 9 - "Here we report the inhibition of TASK-2, TASK-1, TASK-3, TWIK-1 and TRESK by the polyanionic lipids PIP2 and oleoyl-CoA." - not entirely accurate as TWIK-1 and TRESK were not inhibited by PIP2, and TASK-1 was not inhibited by oleoyl-CoA. This is more accurately stated at the beginning of the Discussion.
6. Page 10 - "In the Kir channel family all members (i.e. Kir1.x, Kir2.x, Kir3.x, Kir4.x and Kir5.x) are thought to require PIP2 as mandatory co-factor to be functional (Huang et al., 1998; Logothetis et al., 2007; Furst et al., 2014).", but this should also include Kir6.x and Kir7.x. Also, consider revising the term "mandatory", as there may be good evidence for 2.x, 3.x and 6x, but it is less clear if it is mandatory for the others.
7. Some of the K2P channels such as TRAAK and TALK-2 show large response to PIP2 or oleoyl-CoA. Can the authors comment on the intrinsic open probability of these channels and what the magnitude of modulation one can expect from physiological changes of PIP2 and LC-CoAs?
8. The authors cited previous work by Niemeyer et al., which showed that TASK-2 channels are activated by the short-chain PIP2 derivative dioctanoyl-PIP2. Have the authors tried dioctanoyl-PIP2 at concentrations similar to those used for long chain PIP2 and see whether TASK-2 channels are activated or inhibited in their hands?
9. Readers not experienced in working with PIP2 might find it odd that not all of the traces shown reach a clear steady-state upon perfusion with PIP2, presumably from the accumulation of PIP2 in the membrane. It might be worth including a discussion of the difficulties of achieving an equilibrated system with full-length PIPs, and clarifying exactly how the 'stable current level' referred to in the data analysis section is defined.
10. The authors switch between referring to fold-activation and percentage inhibition (e.g. P6, Fig 1A) - for the sake of comparison it might be simpler to choose one of these descriptors, although this is clearly a choice and up to the authors.
11. The different effect of low (0.1 uM) and high (10 uM) PIP2 concentrations shown in Figure 1D is intriguing. This prompts the question whether the authors could provide further insights into relative PIP2 affinity of different K2P subtypes based on their control recordings. For instance, is there any particular pattern of which K2P subtypes show current run-down under control condition? A related note is whether K2P subtypes that were identified as PIP2 insensitive rather could have a high enough affinity for PIP2 to prevent PIP2 depletion and subsequent current run-down under control conditions. If so, could the lack of response of those K2P subtypes rather reflect that the PIP2 effect is already saturated?
12. Consideration of mechanical effects of introducing PIP2 into an excised cell membrane for the mechanosensitive K2Ps (TRAAK, TREK1/2?) - even very small changes in membrane composition can have observable effects on membrane structure (e.g. Lundbaek and Andersen, 1994; Lundbaek et al. 2004; Veatch et al. 2007). Discerning between mechanosensitive effects and direct PIP2 effects does not seem straightforward given the current experiments - some discussion of this should be included.
13. P10-11 - When discussing the fact that the breakdown of PIP2 appears to be not critical for inhibition of TASK-1/3, Lindner et al 2011 (https://physoc.onlinelibrary.wiley.com/doi/10.1113/jphysiol.2011.208983) is another reference in support.
14. Pharmacological activation of phospholipase C as performed by applying m-3M3FBS results in more complex downstream effects than just reducing PIP2 concentrations, for example, increasing diacylglycerol concentrations as the authors cite in Wilke et al (2014). Discussion of this should be included in the sections regarding the THIK-1 experiments, indicating that the inhibition observed may not necessarily be due to PIP2 depletion.
15. The discussion section about physiological implications: if possible, please discuss how the concentrations of lipids used in this study relates to physiological concentrations of PIP2 and LC-CoA.
16. In the oocyte experiments, the same KCl concentration (120 mM) is used in the intracellular and extracellular solution. The activity of some voltage-gated K channels is influenced by the extracellular K+ concentration. Is this the case also for K2P channels and could this unphysiological extracellular K+ concentration impact the lipid effect?
17. Fig 1A - the choice of a linear, broken scale for fold activation makes it difficult to agree with the authors that the fold-increase in TALK-1/2 and THIK-2 are meaningful - very hard to see the bars and error bars! Maybe the authors could consider a logarithmic scale or other alternatives? The same is true for Fig 2A.
18. Figure 2B: The IV curves for TRAAK and TALK-2 do not seem to cross the 0 xy intercept. Can the authors explain why this is the case?
19. The experiments presented in Figure 3 show that different LC-CoA compounds were applied on the same patch, with a BSA wash-out step in-between each application. Were these experiments always performed with the same order of compounds applied or was the effect dependent on the order of LC-CoA application? We ask this because BSA could potentially bind additional lipid components of the membrane, which could alter the baseline condition in-between LC-CoA applications.
20. Figure 4 - It would be great to also see example traces for TASK-2 and it's mutant. One is included in Fig S1J, but it would seem to be more appropriate here.
21. Table S3: Please comment on the different magnitude of the effect of 3 uM oleoyl-CoA determined in the different data sets (average fold activation of 4.4 and 2.3, respectively). This is a fairly large variability.

REVIEWING TEAM

Reviewed by:

Sara I. Liin, Associate Professor, Linköping University, Sweden: ion channel mechanisms and lipid regulation

Samuel Usher, PhD student at (F.M. Ashcroft lab, University of Oxford, UK): ion channel lipid regulation and fluorescence spectroscopy

Show-Ling Shyng, Professor, Oregon Health & Science University, USA: ion channel function, regulation and structure

Curated by:

Stephan A. Pless, Professor, University of Copenhagen, Denmark

(This consolidated report is a result of peer review conducted by Biophysics Colab on version 1 of this preprint. Minor corrections and presentational issues have been omitted for brevity.)

Endorsement statement (21 September 2021)

The preprint by Heitkamp and Börsch describes visualization of the fast ATP-dependent subunit rotation in reconstituted FoF1-ATP synthase using single-molecule FRET techniques. Using a highly innovative method for trapping single molecules, the authors were able to see the static and dynamic disorder of enzymes in solution, not possible in previous studies. The work makes important contributions to both understanding the structural dynamics of FoF1-ATP synthase and the development of methodologies to study single-molecule dynamics of other proteins in solution.

(This endorsement refers to version 5 of this preprint, which was peer reviewed by Biophysics Colab.)

Consolidated peer review report (18 September 2021)

GENERAL ASSESSMENT

The FoF1-ATP Synthase is the fundamental enzyme that uses the electrochemical potential of protons (pmf) from the electron transport chain to catalyze production of ATP, the currency for energy in our cells. It is also a spectacular nanomachine that works by the rotation of an internal subunit, like an axle, which couples the proton transport by the Fo domain into ATP synthesis by the F1 domain. The coupling is highly efficient, so the enzyme can also act in reverse, as a proton pump that is fueled by ATP hydrolysis. This paper provides a glimpse into the dynamics of the enzyme using single-molecule FRET (smFRET). These authors attached a donor fluorophore (Cy3B) on the rotating ε-subunit and acceptor fluorophore (Alexa Fluor 647) on the static C-terminus of the α-subunit. Upon application of ATP, the ε-subunit is expected to rotate relative to the α-subunit, and transport protons into the vesicle. During the three steps of one rotation, the donor fluorophore is expected to move between one position far from the acceptor, and two positions closer to the acceptor, producing transitions from low to high FRET efficiency with each rotation. To hold the enzyme still during the measurements, the authors use an innovative Anti-Brownian electrokinetic trap (ABEL trap), allowing the them to observe fluctuating rates of functional rotation for individual FoF1-liposomes in solution for extended periods of time (seconds). What they observe is both interesting and unexpected. While the behavior of single molecules is always stochastic, these authors observed about 10-fold differences in the rotation rates from molecule to molecule, a heterogeneity referred to as static disorder, that is not accounted for by stochastic behavior. Using proton ionophores they show that some of this heterogeneity likely results from the buildup of a pmf across the vesicle membrane due to proton pumping in the presence of ATP. However, much of the heterogeneity is not accounted for and awaits further investigation. This preprint provides the groundwork and methodology for those investigations.

Overall, the preprint is a real tour-de-force, requiring intricate membrane protein biochemistry, site-specific fluorescent labeling, single-vesicle trapping, and single-molecule FRET measurements and analysis. The use of the ABEL trap is a particularly powerful innovation that allows them to record a single molecule for a much longer time than previous studies (1 s vs. 10 ms) and, therefore, capture many more cycles of rotation for each molecule. This allowed them to see the static and dynamic disorder of enzymes in solution, not possible in previous studies.

RECOMMENDATIONS

Revisions essential for endorsement:

None

Additional suggestions for the authors to consider:

None

REVIEWING TEAM

Curated by:

William N. Zagotta, Professor, University of Washington, USA

(This consolidated report is a result of peer review conducted by Biophysics Colab on version 5 of this preprint. Minor corrections and presentational issues have been omitted for brevity.)

Consolidated peer review report (26 August 2021)

GENERAL ASSESSMENT

This preprint reports very high-quality structures of the important transporter, ATP13A2. This work will be of interest to those studying membrane transport, especially scientists studying the P-type ATPases but also those in the channel field working on inward rectifier channels where polyamines give rise to inward rectification due to pore block. There seem to be no structures of any channel solved with polyamine bound.

The highlight of the manuscript is the structure with a putative substrate bound in the E2-Pi state. After the current preprint was uploaded, a paper by Li et al was published showing several structures of a yeast homolog, Ypk9 (DOI: 10.1038/s41467-021-24148-y). The pose and coordinating residues are similar to those described by Li et al. It is very interesting to see that this ATPase exploits an approach to recognize and bind polyamines similar to that of bacterial periplasmic polyamine-binding proteins, which have different folds and cellular locations (DOI: 10.1002/pro.5560051004;).

The structures of ATP13A2 in E1 states allow additional understanding of the mechanism and provide some support for a novel mechanism of cytoplasmic polyamine release in which the substrate is released into the cytoplasmic leaflet of the lysosome membrane rather than directly to the cytosol. The Li et al. paper contained only structures in the E2 state, so those authors postulated a half-channel in the E1 state, which this work shows is not there.

This work was commended by the reviewers for the demonstration, by mutagenesis, that aspartate residues in the binding site are required for productive substrate binding and for characterizing the roles of the N- and C-termini by deletion mutagenesis. In particular, the N- and C-termini of some other P-type ATPases act to inhibit ATPase activity, whereas in ATP13A2, ATP hydrolysis is blocked by removal of the C-terminus but unaffected by removal of the N-terminus.

For these reasons, we consider this work to be highly meritorious and we anticipate that it will make an important contribution to the P5B-ATPase field.

RECOMMENDATIONS

Revisions essential for endorsement:

1) The most interesting and novel finding in the manuscript is the evidence that the polyamine substrate may be squeezed out of its binding site into the membrane rather than being released directly to the cytoplasm. According to the conventional thinking about transport by P-type ATPases, the E1 state should have a half-channel from the cytoplasmic surface to the occupied substrate binding site, but the E1 apo structure revealed here has no channel or substrate pocket visible. One explanation might be that there was a transient substrate-bound half-channel which collapsed after substrate dissociation, similar to the one proposed by Li et al. However, the lack of bound substrate in the E1 apo structure argues against this interpretation and also raises the possibility that the substrate is released into the cytoplasmic leaflet of the bilayer. The energetics for such a mechanism appear quite daunting, unless the E2-E1 conformational change disrupts the favorable interactions between bound substrate and the protein, pushing the substrate out of the pocket. Along these lines, does this conformational change cause rotation of the binding site helices in a way that would disrupt favorable interactions between the substrate amino groups and the aspartate residues in the pocket?

Our recommendation is that the manuscript should not take a strong position in favor of either potential mechanism of release without additional evidence, but rather to present both mechanisms as possibilities.

2) The role of the terminal domains in ATP13A2 appears to be unique among P-type ATPases. In several other members of this family, these domains serve an auto-inhibitory function by restricting domain movements. However, neither of the ATP13A2 terminal domains acts this way. The N-terminus associates with the N-domain and the membrane, but its deletion has no effect on substrate-dependent ATPase activity. However, the Li et al paper suggested that the N-terminus was auto-inhibitory in Ypk9 and this might be worthy of some comment. The C-terminal extension associates with the P-domain and is apparently required for substrate-dependent ATPase activity either because it's required for ATPase activity or because its removal prevents the transport process coupled to it. In neither of the truncation mutants does ATPase increase by relieving inhibition. Our recommendation would be to discuss the requirements for N- and C-termini in contrast with other ATPases in which the terminal domains are auto-inhibitory (Ann. Rev. Biophys. (2011) 40: 243-266).

3) The structures revealed a ring of positively charged residues around the interface between protein and lipid on the cytoplasmic surface. This led to the proposal that the region surrounding the putative exit pathway of substrate into the bilayer might be enriched in negatively charged lipids that would help accommodate the released substrate. This feature was not commented on in the paper on the Ypk9 structure. Is it possibly just a fortuitous difference unrelated to mechanism? We recommend that the authors comment on sequence differences between human ATP13A2 and yeast Ypk9 in that region. Mutagenesis experiments could be performed to decrease positive charge in the region adjacent to the putative exit pathway for substrate into the cytoplasmic leaflet. However, the reviewers realize that this might involve much more work than appropriate for inclusion with this manuscript.

4) The discussion compares P5A and P5B ATPases with the assumption that the substrates for P5A ATPases are mis-targeted N- or C-termini of terminally anchored membrane proteins. Although there is evidence consistent with this function, it has not been demonstrated that P5A ATPase activity is dependent on those mistargeted domains, which still leaves the possibility open that the effect is indirect. The reviewers recommend rewriting this part of the discussion in a way that does not imply that mistargeted terminal domains have been proven to be substrates for P5A ATPases.

5) As a matter of terminology, occluded states of P-type ATPases, like other transporters, refer to conformations in which the substrate is bound but unable to dissociate because the binding site is closed off to either side of the membrane. This manuscript refers to a substrate-free E1 structure as "occluded". It would be better described as an "empty" or "apo" state.

Additional suggestions for the authors to consider:

None

REVIEWING TEAM

Reviewed by:

Wei Mi, Assistant Professor of Pharmacology, Yale University, USA: structural biology, ABC transporter mechanisms

Michael Broberg Palmgren, Professor, University of Copenhagen, Denmark: mechanism of P-type ATPases

Gary Rudnick, Professor of Pharmacology, Yale University, USA: mechanism of ion-coupled transporters, biochemical determination of conformational changes

Curated by:

Gary Rudnick, Professor of Pharmacology, Yale University, USA

(This consolidated report is a result of peer review conducted by Biophysics Colab on version 1 of this preprint. Minor corrections and presentational issues have been omitted for brevity.)

Consolidated peer review report (3 September 2021)

GENERAL ASSESSMENT

Cystic Fibrosis (CF) is a lethal genetic disease, caused by loss-of-function mutations in the cftr gene that encodes the epithelial ion channel CFTR (Cystic Fibrosis Transmembrane conductance Regulator), a mediator of chloride and bicarbonate transport across the cell membrane. In the past decade, we have witnessed the success of precision medicine strategies in CF clinics using small-molecule compounds targeting directly the CFTR protein. These drugs improve folding, maturation, stability and gating at the plasma membrane of mutant CFTR versions. The objective of this study is to improve our molecular understanding of how one type of these drugs, Class I correctors, specifically lumacaftor, VX-809, and tezacaftor, VX-661, work on CFTR.

The manuscript describes three new cryo-electron microscopy structures of CFTR: both nucleotide-free (channel closed state) and ATP-bound (channel active state) lumacaftor-bound structures, and an ATP-bound tezacaftor-bound structure. All three structures show that type I correctors bind in the same small cavity at the cytoplasmic edge of the membrane of the first transmembrane domain, although the binding modes of the two drugs are slightly different within the site. The authors both confirm the location of binding site and find evidence for the distinct binding specificity of the two drugs by identifying mutations within this cavity that decrease the drugs' binding affinity and effectiveness of improving ΔF508-CFTR (the most common CF-causing mutation) folding in a cell-based assay. The results of these biochemical experiments are consistent with their structural observations, providing solid evidence that the binding pocket that is observed in is the one targeted by type I correctors to improve CFTR folding efficiency.

The strength of the paper lies in the clarity and consistency of the structural data with maturation and binding assays, as well as with much of the existing literature. The three presented structures are consistent, making for strong evidence of the proposed mechanism for type I correctors, namely that they stabilize the transmembrane domain 1, enabling a larger proportion of the CFTR molecules to overcome the slow, defective folding of other domains, and of the whole CFTR protein overall. The manuscript includes a scholarly discussion of previous related literature that effectively adds support to the conclusions and illustrate how their new results are consistent with and help explain many previous observations. References to additional literature, as detailed in our recommendation, could further enhance the discussion.

The manuscript provides evidence that other corrector types do not use the binding site they identify for type I correctors, but does not resolve their mechanism. It will therefore be exciting in future studies to use similarly elegant approaches to elucidate the mechanisms of action for other corrector types postulated to work through distinct mechanisms. Altogether, this work reflects a rigorous presentation of an investigation into the mechanism for type I correctors, and the current manuscript will be of great interest to many in the fields of cystic fibrosis, protein folding, and drug design. The reviewing team has the following minor recommendations to improve clarity of the presentation of these results.

RECOMMENDATIONS

Revisions essential for endorsement:

None

Additional suggestions for the authors to consider:

1) Expand on background. Stating in the introduction, rather than later in the manuscript, that F508 is in NBD1 could help better convey the allostery argument made in the discussion that binding of a corrector in the TMD rescues the folding of a mutation in the NBD. At the end of the introduction, the phrase "support a specific mechanism of action" is ambiguous or vague. Do the authors mean that the mechanism is through specific interaction with CFTR (as opposed to a model where the drug acts indirectly by modifying membrane properties, as suggested earlier in that paragraph)? In general, it would be more effective summarize the actual mechanism. Page 11: WT CFTR may not traffic to the cell membrane efficiently in heterologous expression systems as reported previously, but they are processed far better in native epithelial cells.

2) Expand on visual detail in the binding site. Enlarge the frame of Figure 2C and Figure 3B so that the side chain densities for K68 and R74 can be included. Some detailed description of the interaction between residues 371-375 and N66 and P67 may be warranted since lumacaftor can improve surface expression of P67L, a folding defective mutant. It would be helpful to include a figure panel that illustrates the interactions between TM1 and TM6 (and the molecules), perhaps in Figure 2E. Showing these interactions explicitly could help readers see the clasp between TM1 and TM6 that is later invoked when proposing the mechanism of action of type I correctors.

3) Correctors also stabilise ΔF508-CFTR once fully folded and at the membrane. The authors state (page 3): "chaperones that increase the amount of folded CFTR are called correctors" and "some cause defects in channel function and others interfere with CFTR expression and folding". Most mutations, including ΔF508, interfere with both biogenesis and channel function. Also later "Patients with folding mutations..." Most folding mutations also cause gating impairment, justifying a combination therapy with both potentiator and corrector. Correctors are defined in a more pragmatic way as increasing the amount of CFTR at the plasma membrane - whether they act as chaperones (specifically helping with folding) or through stabilization of the protein at the membrane. Throughout the manuscript the authors only consider the action of class I correctors on CFTR folding. However, there is evidence that mature deltaF508-CFTR stability at the plasma membrane is also increased by VX-809 (Eckford et al. Chem Biol. 2014; Meng et al., J Biol Chem 2017). This should be mentioned and discussed.

4) Cavity in which correctors bind: could this aspect of the data be used to give further insight? On page 11, the authors point out that there is a relatively large cavity into which the correctors can fit, without altering CFTR conformations. The empty cavity is predicted to destabilize CFTR. However, a similar-sized space is present in TMD2, lined by the elbow helix of TM7, TM9 and TM12. Does this TMD2 cavity also destabilize CFTR? Might correctors rationally designed to fill that space act in synergistic with class I correctors? The effect might be smaller, but even the more C-terminal TMD2 could impact on NBD2 folding, and on stability of the mature protein. Might it be interesting to perform more analysis, comparing size and hydrophobicity of the two cavities?

5) Link between early stabilization of TMD1 and overall efficacy of maturation is supported by published biochemical data. On page 12, the authors state"As CFTR folding is a highly cooperative process, stabilizing TMD1 would ultimately increase the overall probability of forming a fully assembled structure and thereby allosterically rescue a large number of disease-causing mutants that reside in other parts of CFTR." The Braakman lab (Kleizen et al. JMB, 2021) show that the early effect of VX-809 on TMD1 stability correlates with an increase in total mature protein - consistent with reduced degradation at early stages, and cooperativity of conformational maturation (with an early stabilization of the TMD1/NBD1 interface positively affecting folding and assembly of downstream domains). In addition, mutations shown to render CFTR "hyper-responsive" to VX-809 are all linked to the VX-809 binding site presented here via secondary structure elements - P67L (via lasso helix), E92K (via TM1) and K166E and R170E (via TM2). It is plausible that these mutations worsen the intrinsically slow TMD1 packing, ER-membrane insertion and downstream biogenesis steps that correctors can accelerate. Readers may appreciate reading more details of how the structural data presented here is confirmed by these functional biochemical analyses.

6) Synergy of class I correctors with suppressor mutations could be explained better. On page 12, the authors state: "This mechanism is also consistent with the synergy between lumacaftor and suppressor mutations (Farinha et al., 2013; Okiyoneda et al., 2013): lumacaftor extends the lifetime of TMD1 and the suppressor mutations stabilize different parts of CFTR or enhance inter-domain assembly, and thus together they achieve higher rescuing efficiency". This could be explained a bit better. Several papers demonstrate that the effect of VX-809 is less than additive with the effect of the second-site revertant R1070W mutation on ΔF508-CFTR (He et al., 2013 FASEB J; Okiyoneda et al., 2013 Nat Chem Biol). This seems to contradict the sentence above. However, the non-additivity is consistent with the mechanism the authors propose. According to the latter, correctors stabilize TMD1. This in turn stabilizes the TMD1/NBD1 interface, which provides a "nucleus" which helps folding of downstream domains, post-translational domain assembly and strengthens the functionally important TMD/NBD1 ball-and-socket joint. The R1070W revertant mutation provides molecular contacts at the NBD/TMD interface. Thus both rescue strategies affect similar steps in CFTR's maturation and improve interdomain interactions at, and stability of, the same interface. This overlap in mechanism likely explains the reduced effectiveness of the combination (corrector+revertant mutation). On the other hand, most other suppressor mutations stabilize NBD1. These have a very distinct mechanism and therefore a clear synergistic effect with VX-809.

7) Interpretation of the conformational state of CFTR. Electrophysiological studies indicate that the phosphorylated, ATP bound CFTR is expected to have open probabilities close to 1, and yet, no transmembrane permeation pathway has been found in structures under these conditions (PDB ID: 6MSM, Zhang et al., 2017 Cell, and the structures in this paper). Previously, the authors speculated that this might be related to some distortion in the membrane-embedded TMDs in the cryo-EM structures. Since the drug-binding site described here is at the protein-lipid interface, how might these distortions impact the interpretation of your results? In addition, among all the structures of CFTR published so far from the authors' group, the apo states show lower resolution than the phosphorylated, ATP-bound states. It would be useful to understand how these inherent differences in structure determination might affect the overall interpretation.

8) Expand on cryoEM methods. It would be helpful if the authors could provide some more explanations for Figure S5. For example, please explain the rationale for collecting three sets of 3D classes; What criteria did the authors use to pool the three green classes into one? How did the duplicated particles get removed? Please specify the condition for grid freezing or reference to previous publications.

9) Expand on binding assays. In the methods, it would be helpful to specify whether the proteins used in the SPA assay were purified in the same way as the proteins used for the cryoEM (using both anti-GFP affinity chromatography in LMNG+CHS and SEC in digitonin), or whether a different protocol was used. In the first results section, the authors compare the Kd values that they obtained to previously published EC50 values. They refer to these previous experiments (by Van Goor et al 2016, Van Goor et al 2011, and Ren et al 2013) as "in vivo". But all these results were in fact in vitro, in cell-based experiments (and described as such in the original papers).

10) Figure S6B is not discussed anywhere in the text, and it should be at least mentioned in the main text or the methods section. Is the extra density, attributed to a lipid acyl chain, present only in this specific structure? Also, the density seems rather large in diameter for an acyl chain. Are other acyl chains visible elsewhere in the structure and how do they compare?

REVIEWING TEAM

Reviewed by:

Rachelle Gaudet, Professor, Harvard University, USA: structural biology of membrane proteins, ABC transporters and Nramp-family transporters, cadherin-family protein structure and assembly

Tzyh-Chang Hwang, Professor, University of Missouri, USA: structure and function of CFTR, CFTR pharmacology, electrophysiology

Paola Vergani, Associate Professor, UCL, UK: CFTR structure-function, CFTR pharmacology, epithelial physiology

Curated by:

Janice L. Robertson, Assistant Professor, Washington University in St. Louis, USA: membrane protein folding & stability, single-molecule microscopy, computational modeling

(This consolidated report is a result of peer review conducted by Biophysics Colab on version 1 of this preprint. Minor corrections and presentational issues have been omitted for brevity.)

Authors' response (6 August 2021)

GENERAL ASSESSMENT

This manuscript reports the development of a single molecule (SM) approach for studying individual ligand binding events for a membrane protein in a native lipid membrane environment. The authors express the eukaryotic TAX-4 cyclic nucleotide-gated channel in mammalian cells tagged on their cytoplasmic N-terminus with EGFP, form nanovesicles using nitrogen cavitation, separate the plasma membrane fraction from ER vesicles using gradient ultracentrifugation and then purify the fraction of vesicles containing TAX-4 oriented with its intracellular domains outward using GFP nanobodies immobilized onto cover slips. To visualize binding and unbinding of an agonist at the SM level, the authors utilize low concentrations of the fluorescent cGMP analog fcGMP along with TIRF microscopy. The authors develop the approach in a nuanced and cautious fashion, with nice controls to demonstrate that the preparation works for the TAX-4 channel, but also for a more complex assembly of GABA receptors comprised of alpha1, beta2 and gamma subunits. Adsorption of both TAX-4 and GABA receptors appears to be specific as fluorescent puncta are not observed without the GFP nanobody. In the case of TAX-4, many EGFP-positive puncta are observed that do not bind fcGMP, indicating that not all channels remain functional. fcGMP puncta are also observed that do not contain EGFP fluorescence, indicating that fcGMP can adhere to coverslips non-specifically. However, single binding events of fcGMP to EGFP-positive puncta can be readily observed, they can be competed out using cGMP, and both binding and unbinding events were analyzed quantitatively. The authors demonstrate that bound lifetimes are independent of agonist concentration, whereas unbound lifetimes decrease as agonist concentration increases, as would be expected if they are able to resolve individual binding and unbinding events. Bound lifetimes are poorly described by single exponential functions over a range of fcGMP concentrations, suggesting that TAX-4 channels have at least two distinct bound conformations. The authors explore a range of binding models to account for their results and find that their results are consistent with a model in which the nucleotide binding domain alternates between an open conformation that can bind and unbind agonist, and a closed conformation that hinders both binding and unbinding. The authors hypothesize that the conformational change correspond to an early step in the activation process, agreeing with cryo-EM structures of TAX-4 in the absence and presence of agonist. The modeling and interpretation of results is nuanced and presented in an open and objective fashion, although more details on the modeling would be helpful. The author also study double-bound events and uncover evidence that unbinding of the second ligand is slower than the first, suggesting positive cooperativity between the first and second agonist binding events. Overall, the methodology is well described, and the controls certify the quality of the data shown. The authors explain the limitations of the technique and restrict their focus to the two initial binding event and do not draw conclusions on the nature of the conformational change or whether the conformational change correspond to individual subunits or all subunits at the same time. Despite these limitations, the manuscript beautifully describes an elegant approach for studying ligand binding dynamics at the SM level and the possible relationship with conformational changes while the molecule is embedded in the physiological membrane. The following are suggestions the authors should consider when revising the manuscript.

RECOMMENDATIONS

Revisions essential for endorsement:

• The authors should provide statistics on the number of colocalized spots compared to the number of non-colocalized GFP and fcGMP spots in GABA vs TAX-4. As seen in the GABA negative controls, colocalization does occasionally occur spuriously. It would be ideal to show this type of quantitation for experiments done on different days and with different vesicle preps to give the reader a sense of the frequency of binding competent channel proteins are observed and whether there is day to day variability. 60 hours of binding dynamics is also not a very useful statistic. Please provide the number of traces/replicates/individual vesicle preparations in the figure legends.

We agree with the reviewers that statistics for overall number of experimental preps and spots vs. colocalized spots would be informative. Number of colocalized single molecules at each concentration in the final dataset: 10 nM: 112, 30 nM: 325, 60 nM: 63, 100 nM: 65, 200 nM: 132. In lieu of including this information in nearly every figure caption, we provide it in the Methods (page 26, line 9). Data were collected from four separate experimental preparations. However, there is also a fair degree of variability in the nonspecific binding observed at different locations even within a single chip. We did some manual selection at low laser power for areas with low background GFP fluorescence to attempt to record from the best spots in a chip, but we did not attempt a thorough search as this would necessarily also bleach GFP molecules needed for bleach step analysis. We attribute this variability to nonuniformity in the pacification PEG layer. In addition to the GABA control, we have also now done controls with a TRP channel containing an intracellular GFP. In these controls far fewer colocalized spots (~7%) were observed than with TAX-4 (30-40%) across all four preps. Although we agree that number of molecules/preps are informative, we disagree that the total recording time is not a useful piece of information. Indeed, for dynamics we would argue that it is one of the most important pieces of information and highlights a strength of our approach in that binding of fresh fcGMP allows long duration 4-7 min. recordings of individual molecules.

We have merged Supplementary Figs. 4 and 5 (these are now all in Supp. Fig. 4) and added a new Supplementary Fig. 5 comparing colocalization statistics along with exemplar images for vesicles with GFP-TAX-4 and controls for vesicles with a TRPV1 channel containing an intracellular GFP. These data clearly show consistent colocalization only in the presence of TAX-4-GFP.

• The authors prefer a model wherein a conformation change prevents the binding and unbinding of agonist. The authors explanation of their thinking and the exclusion of model M1.F wasn't always easy to follow. It would helpful if the authors provided a somewhat more complete explanation for why the model with the lower BIC is not the preferred and what constants are significantly lower to make the model M1.F worse than M1.E. This is important because this is used to discard binding and unbinding after the conformational change and support the hypothesized conformational change. Have the authors explored the possibility that the conformational changes detected are intermediate states different to the final state with the four binding sites occupied?

This is an important point. Regarding M1.E vs M1.F, as expected for a model with an extra degree of freedom the BIC for M1.F is lower. However, it's only marginally lower, suggesting that the additional degree of freedom wasn't hugely beneficial. Furthermore, the binding and unbinding rates following the conformational change in M1.F are an order of magnitude slower than those preceding it, the rates for which match very well with M1.E (see Table S2). Although it is not our intention to completely rule out binding/unbinding after the conformational change, it seems that it is at least inhibited, and thus we opt for the simpler model lacking these transitions. We have added several sentences near the bottom of page 11 to clarify this.

Additional suggestions for the authors to consider:

• Do the authors have any additional data to inform on how well gradient ultracentrifugation enriches the PM fraction? Have the authors probed fractions with antibodies against ER resident proteins or those in other intracellular organelles?

We did not additionally probe for ER proteins as was done previously (Fox-Loe et al., 2017). However, our results for the PM fraction match those in this prior study.

• Quantifying fcGMP photobleaching rates based on those that are nonspecifically adsorbed to the surface probably isn't the most robust method. Dyes stuck to the surface will likely encounter higher intensities in the evanescent field due to their proximity to the surface and will often also have distorted photophysical properties as is observed in the traces shown. A better method would be to encapsulate fcGMP in vesicles and measure bleaching rates.

We agree that dyes on the surface are likely to bleach more quickly, if anything, than dyes tracking binding events. However, this makes it a nice extreme limit control. If even these bleach times are long compared to our observed binding events, then it's unlikely that bleaching is grossly altering our observed dynamics. Regarding encapsulating dyes in vesicles, although this could be fruitful it also brings some complications. If the vesicle size is not tightly controlled (and even if it is) then there could be a significant excitation gradient across the vesicle that may lead to longer times to bleaching than would be observed at the binding site.

• The distribution in individual fcGMP intensities observed could be caused by irregularities in the laser illumination spot or the emission pathway though this is limited in mmTIRF setups generally. The authors should comment on this in the methods.

Nonuniformities in the optical excitation or emission paths would lead to spatial variation in fcGMP intensities, but not variation at a single site. The laser intensity is stable in time as judged by both background readings away from any identified spot and separate tests with a power meter, so it is unlikely to be due to artifactual fluctuations in laser power. The variability we observe likely requires some sort of dynamics at the site in question involving either a relative motion in the TIRF field gradient or photodynamics of the dyes themselves.

• Have the authors considered whether it might be possible to do experiments with APT-cGMP or another analog for covalent ligand attachment to two of the CNBDs while the others are activated by fcGMP? This might be a useful way to examine agonist binding steps beyond the first two given the limitation of having to use low agonist concentrations.

This is a great suggestion that we will investigate. We also have some similar ideas that we are currently pursuing in this regard.

• The authors don't comment on whether the conformational change can occur in absence of ligand binding, a possibility included in the models. This event cannot be detected with this methodology but are relevant for the relationship of the conformational changes and gating of the channel and can modify the binding kinetics detected but not the unbinding kinetics. It would be helpful if the authors discuss uncertainties created by not knowing the extent to which the conformational change does or does not occur in the absence of agonist.

Actually, we can detect this with the current methodology: analysis of unbound dwell times suggests multiple components consistent with at least two unbound states. Indeed, our favored single site model M1.E includes such a conformational change. This was also the case for our prior observations in isolated CNBDs from HCN channels. Thus, we do believe that this occurs. However, the rates for the conformational change are much slower in the absence of bound ligand (Table S2). For this reason, and because the models would otherwise have been too complex, we ignored this transition in models of two binding sites. We have amended the text near the top of page 12 to clarify this.

• The inside-out orientation appears to work robustly for the TAX-4 channel. Can the authors comment in the discussion on potential intracellular mechanisms known to regulate TAX-4 or other cyclic nucleotide-gate channels that might be disrupted in this orientation? Many channels are regulated by PIP2, which would be depleted in the inside-out orientation.

This is an interesting question, and we acknowledge that despite retaining the channel in the cell membrane, the vesicle preparation is not exactly a native environment. We also acknowledge that we did not control for any intracellular factors such as PIP2 that could regulate the binding dynamics. Intracellular PIPs are known to reduce apparent affinity of CNG channels for cGMP and to inhibit maximal current. Indeed, our approach could potentially provide some insight into which transitions were preferentially affected upon addition of PIP2 if it is largely absent from the vesicle prep, or any other intracellular factor for that matter.

(This is a response to peer review conducted by Biophysics Colab on version 1 of this preprint.)

Endorsement statement (30 August 2021)

The preprint by Patel et al. describes the development of a single molecule approach for studying individual ligand binding events in membrane proteins within native lipid environments. The approach represents an elegant way to investigate the dynamics of ligand binding, and potential relationships with conformational changes, in molecules embedded within physiological membranes. The work makes an important contribution that will be of interest to scientists working on molecular mechanisms in ion channels and other membrane proteins.

(This endorsement by Biophysics Colab refers to version 2 of this preprint, which has been revised in response to peer review of version 1.)

Consolidated peer review report (23 July 2021)

GENERAL ASSESSMENT

This manuscript reports the development of a single molecule (SM) approach for studying individual ligand binding events for a membrane protein in a native lipid membrane environment. The authors express the eukaryotic TAX-4 cyclic nucleotide-gated channel in mammalian cells tagged on their cytoplasmic N-terminus with EGFP, form nanovesicles using nitrogen cavitation, separate the plasma membrane fraction from ER vesicles using gradient ultracentrifugation and then purify the fraction of vesicles containing TAX-4 oriented with its intracellular domains outward using GFP nanobodies immobilized onto cover slips. To visualize binding and unbinding of an agonist at the SM level, the authors utilize low concentrations of the fluorescent cGMP analog fcGMP along with TIRF microscopy. The authors develop the approach in a nuanced and cautious fashion, with nice controls to demonstrate that the preparation works for the TAX-4 channel, but also for a more complex assembly of GABA receptors comprised of alpha1, beta2 and gamma subunits. Adsorption of both TAX-4 and GABA receptors appears to be specific as fluorescent puncta are not observed without the GFP nanobody. In the case of TAX-4, many EGFP-positive puncta are observed that do not bind fcGMP, indicating that not all channels remain functional. fcGMP puncta are also observed that do not contain EGFP fluorescence, indicating that fcGMP can adhere to coverslips non-specifically. However, single binding events of fcGMP to EGFP-positive puncta can be readily observed, they can be competed out using cGMP, and both binding and unbinding events were analyzed quantitatively. The authors demonstrate that bound lifetimes are independent of agonist concentration, whereas unbound lifetimes decrease as agonist concentration increases, as would be expected if they are able to resolve individual binding and unbinding events. Bound lifetimes are poorly described by single exponential functions over a range of fcGMP concentrations, suggesting that TAX-4 channels have at least two distinct bound conformations. The authors explore a range of binding models to account for their results and find that their results are consistent with a model in which the nucleotide binding domain alternates between an open conformation that can bind and unbind agonist, and a closed conformation that hinders both binding and unbinding. The authors hypothesize that the conformational change correspond to an early step in the activation process, agreeing with cryo-EM structures of TAX-4 in the absence and presence of agonist. The modeling and interpretation of results is nuanced and presented in an open and objective fashion, although more details on the modeling would be helpful. The authors also study double-bound events and uncover evidence that unbinding of the second ligand is slower than the first, suggesting some positive cooperativity between the first and second agonist binding events. Overall, the methodology is well described, and the controls certify the quality of the data shown. The authors explain the limitations of the technique and restrict their focus to the two initial binding event and do not draw conclusions on the nature of the conformational change or whether the conformational change correspond to individual subunits or all subunits at the same time. Despite these limitations, the manuscript beautifully describes an elegant approach for studying ligand binding dynamics at the SM level and the possible relationship with conformational changes while the molecule is embedded in the physiological membrane. The following are suggestions the authors should consider when revising the manuscript.

RECOMMENDATIONS

Revisions essential for endorsement:

1) The authors should provide statistics on the number of colocalized spots compared to the number of non-colocalized GFP and fcGMP spots in GABA vs TAX-4. As seen in the GABA negative controls, colocalization does occasionally occur spuriously. It would be ideal to show this type of quantitation for experiments done on different days and with different vesicle preps to give the reader a sense of the frequency of binding competent channel proteins are observed and whether there is day to day variability. 60 hours of binding dynamics is also not a very useful statistic. Please provide the number of traces/replicates/individual vesicle preparations in the figure legends.

2) The authors prefer a model wherein a conformation change prevents the binding and unbinding of agonist. The authors explanation of their thinking and the exclusion of model M1.F wasn’t always easy to follow. It would helpful if the authors provided a somewhat more complete explanation for why the model with the lower BIC is not the preferred and what constants are significantly lower to make the model M1.F worse than M1.E. This is important because this is used to discard binding and unbinding after the conformational change and support the hypothesized conformational change. Have the authors explored the possibility that the conformational changes detected are intermediate states different to the final state with the four binding sites occupied?

Additional suggestions for the authors to consider:

1) Do the authors have any additional data to inform on how well gradient ultracentrifugation enriches the PM fraction? Have the authors probed fractions with antibodies against ER resident proteins or those in other intracellular organelles?

2) Quantifying fcGMP photobleaching rates based on those that are nonspecifically adsorbed to the surface probably isn’t the most robust method. Dyes stuck to the surface will likely encounter higher intensities in the evanescent field due to their proximity to the surface and will often also have distorted photophysical properties as is observed in the traces shown. A better method would be to encapsulate fcGMP in vesicles and measure bleaching rates.

3) The distribution in individual fcGMP intensities observed could be caused by irregularities in the laser illumination spot or the emission pathway though this is limited in mmTIRF setups generally. The authors should comment on this in the methods.

4) Have the authors considered whether it might be possible to do experiments with APT-cGMP or another analog for covalent ligand attachment to two of the CNBDs while the others are activated by fcGMP? This might be a useful way to examine agonist binding steps beyond the first two given the limitation of having to use low agonist concentrations.

5) The authors don’t comment on whether the conformational change can occur in absence of ligand binding, a possibility included in the models. This event cannot be detected with this methodology but are relevant for the relationship of the conformational changes and gating of the channel and can modify the binding kinetics detected but not the unbinding kinetics. It would be helpful if the authors discuss uncertainties created by not knowing the extent to which the conformational change does or does not occur in the absence of agonist.

6) The inside-out orientation appears to work robustly for the TAX-4 channel. Can the authors comment in the discussion on potential intracellular mechanisms known to regulate TAX-4 or other cyclic nucleotide-gate channels that might be disrupted in this orientation? Many channels are regulated by PIP2, which would be depleted in the inside-out orientation.

REVIEWING TEAM

Reviewed by:

Gabriel Fitzgerald, Postdoctoral Fellow (J.A. Mindell lab, NINDS, USA): membrane protein mechanisms, single molecule spectroscopy

Pablo Miranda, Staff Scientist (M. Holmgren lab, NINDS, USA): ion channel mechanisms, electrophysiology, fluorescence spectroscopy

Kenton J. Swartz, Senior Investigator, NINDS, USA: ion channel structure and mechanisms, chemical biology and biophysics, electrophysiology and fluorescence spectroscopy

Curated by:

Kenton J. Swartz, Senior Investigator, NINDS, USA

(This consolidated report is a result of peer review conducted by Biophysics Colab on version 1 of this preprint. Minor corrections and presentational issues have been omitted for brevity.)