From the journal RSC Chemical Biology Peer review history

06-Oct-2020

Dear Dr Chattopadhyay:

Manuscript ID: CB-ART-08-2020-000145
TITLE: Membrane composition and lipid to protein ratio modulate amyloid kinetics of yeast prion protein

Thank you for your submission to RSC Chemical Biology, published by the Royal Society of Chemistry. I sent your manuscript to reviewers and I have now received their reports which are copied below.

After careful evaluation of the manuscript and reviewers’ comments, I regret to inform you that I do not find your manuscript suitable for publication and therefore it has been rejected in its current form.

However, if you are able to fully address the concerns raised by the reviewers in the reports below, I will consider a substantially rewritten manuscript which takes into account all of the reviewers’ comments. If you choose to resubmit your manuscript, please include a point by point response to the reviewers’ comments and highlight the changes you have made.

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************

Reviewer 1

Arnab et al, report that the NM region of Sup35 exhibits an interesting biphasic aggregation kinetics within a regime of lipid/protein ratio between 20:1 and 70:1. In the presence of low or high lipid concentrations, the aggregation kinetics is found to be monophasic again. The present data using conventional and single molecule spectroscopy show interesting correlation lipid to protein ration, membrane binding affinity and protein aggregation and show that a competition between protein-lipid and protein-protein interactions is responsible for the bi-phasic nature of the aggregation kinetics. Overall the manuscript is well conceptualized and technically strong, however, requires some important aspects be addressed through better interpretation and refinement of the results/discussion, after which I think it should be considered for publication.

Comments to be addressed:

1) Figure 2:
a) What is the time scale of the incubation of the sample for the measured/reported rH1 and rH2 data in Fig 2C? Assuming that when Sup35 is incubated with lipid vesicles, in principle, there is an ensemble of the following three population - free vesicles (ruled out as they are unlabeled), protein bound vesicles and protein-protein aggregate (multimer). So, in case of the shown rH2 of the membrane bound protein - how do the authors rule out the existence of protein-protein aggregates? Perhaps, this could be ameliorated by mentioning the time scale.

b) It is not clear how was the % of the bound/free Sup35 determined shown in Fig 2D? I am assuming it has been extracted from the rH data from the FCS experiments. The authors should elaborate on this either in the method part or in the results for ease of understanding.

2) Figure 4:
It is not clear what is the concentration of Sup35 used for the ThT assay. At one point the authors do mention that 30uM of the protein was used for aggregate preparation. Is this the concentration of the protein used for all ThT kinetics?

3) Figure 5:
Figure 5 and 6, taken together show FCS and AFM data on the basis of which the model is proposed in Fig 7. While the data shown are quite interesting, however, the interpretation in some parts requires more clarity. The proposed model also needs some refinement as reported data does not seem to sufficiently back the claim, or might be little too extrapolated. Particularly, some of the issues that need more clarity are -

a) Figure 5D shows that the avg diffusion time remains largely unchanged till about 50-70hrs, suggesting the aggregation of the free protein is slow (i.e, remains monomeric largely). Fig 5E, (OLC + protein) shows a gradual slowing down in the diffusion time over 0 to 70 hrs and beyond, suggesting some sort of interaction - either vesicular fusion or protein bound to vesicle. What is not clear is how do the authors explain the observation that while avg diffusion time is increasing (slowing down), the population of monomeric protein as well membrane bound protein remains largely unchanged during 0-70hrs (Fig 5H)? Authors should discuss this aspect more clearly.

b) The avg diffusion time in Figure 5F seems to be similar to the monomeric Sup35NM diffusion time shown in Figure 5D, which doesn’t support the conclusion that the authors arrive at, that at ELC the protein forms aggregates that are membrane bound and increase in size on prolonged incubation. Authors should take note of this and revisit the interpretation and discussion appropriately.

c) Does Figure 5I corresponds to reflect the population of protein-protein aggregate or the monomeric protein? It is not clear from the reported information.

4) The model proposed in Figure 7 is interesting but has some ambiguity and needs further refinement in my view. Particularly, in case of the OLC at 100hr the model is misleading. The authors propose that protein-protein aggregate is predominant in comparison to membrane bound fibril. Their claim is based on the binding affinities obtained from ITC, however, the dye leakage also shows leakage within 10 minutes of protein incubation suggesting strong binding. From this observation how can the authors rule out that the protein does not bind to vesicles (under OLC) until 80hrs or so? Infact the data shown does seem to suggest that at 100hr (Fig. 5H), there is roughly equal populations of protein-protein aggregates and membrane bound protein (could be bound multimer or fibril too). Therefore, to claim that around 100hrs protein-protein aggregate predominate in incorrect in my view and I suggest author revisit and tone down the conclusions drawn.
I would think the protein would bind to the vesicles, however, the nucleation/fibrillation over the vesicle surface is very slow perhaps due to pore formation on the vesicle destabilizing the fibril formation. Over time some of the vesicle will fuse resulting in more stable and creation of larger surface area that would then allow further fibrillation to take place supporting the biphasic observation.



Minor:

1) Page 4, Para 2, Line 4: Authors should adhere to the complete nomenclature of the lipids used. PC/PS are just the head groups.

2) PS based lipids are apoptotic markers and not present in the outer leaflet of the cell membrane. Citations 18,34 cited in the introduction supporting the presence of DMPS in outer-leaflet are incorrect and don’t seem relevant. PS can be used as a model negatively charged lipid and therefore, the sentence needs correction.

3) The presentation of the Fig 2A in the current form does not give away much information except for a schematic. Since the authors have computationally modelled the structure of the protein, determined the interacting regions and the free energies, the figure can be improved by highlighting the lipid interacting (or membrane inserting) region of the modeled protein in the current figure as well as including the free energies of interaction as a table in supporting information.

4) Page 12, first line: ….” We determined the values ---- with lipid concentrations for protein in the absence of lipid. A typo needs correction.

5) Figure S6, the plot for the dye leakage assay shows “Sup35NM only”. What do the authors mean by the this? Or is this a negative control of SUV only which has been wrongly labeled? Either way SUV should not show any leakage in the absence of protein over a period of 600 seconds.

6) Most figure axis major/minor ticks/labels are not clearly visible. The authors should use a larger font size for labeling.

Reviewer 2

The manuscript by Bandyopadhyay et al. describes the aggregation of a yeast prion protein namely, Sup35NM upon binding to a membrane that was investigated using a host of biophysical techniques such as far-UV CD, ThT assay, Fluorescence Correlation Spectroscopy (FCS), AFM, and calcein release assay in addition to cytotoxicity studies. Based on the findings, the authors conclude that both lipid composition and lipid/protein ratio play a critical role in triggering Sup35 aggregation. At optimum zwitterionic lipid concentration, Sup35 exhibits biphasic aggregation kinetics whereas, at both low and high lipid concentrations, Sup35 follows monophasic kinetics. However, unlike mammalian prion protein (which is lipid-anchored and misfolding is influenced by lipid composition), is there any biological relevance of lipid-induced aggregation of the yeast prion protein? I believe this issue must be adequately addressed. Hence, I leave the assessment of the suitability of this work at a Chemical Biology journal at the discretion of the Editor. Additionally, although the current work is exhaustive, it lacks rigorousness in the experimental details and some detailed rationale. For the benefit of the authors, I summarize my comments as follows.

1. It is still not clear to me what pertinent role does the lipid play in Sup35 aggregation. Has the physiological relevance of lipid-induced Sup35 aggregation been demonstrated/documented in yeast? Although the authors have mentioned that Sup35 serves as a model prion protein but their implications are completely in contrast to each other.

2. The authors should either provide the entire Sup35NM sequence or mention the amino acids present within the sequence stretch 130-143 as they infer from the OPM results that this flexible region/stretch is a potential membrane-binding region. At least it will give an idea about the nature of amino acids that interact with DMPS. The corresponding Fig. 2A caption must indicate the significance of various color codes shown in membrane-bound Sup35NM.

3. In the Materials and methods section, it has been mentioned that the liposomes, obtained after extrusion using 80 nm and 120 nm pore filters, exhibited an average diameter of 200 nm. I find this quite unusual! How many times the extrusion was carried out? Also, shall the liposomes of an average diameter of 200 nm be still considered as SUVs? Isn’t the name LUVs more appropriate?

3. Fig. 3 B-D: What was the concentration of Sup35NM and the overall lipid concentration for FT-IR studies? This should be mentioned in the Materials and Methods section as well as in the figure caption. The absorbance values differ in all of the three figures. A careful look and subsequent comparison of the fig. 3B and 3D do not reveal a significant difference in the area (shaded regions) of -helix and -sheets. The authors should comment on the observed similarities/dissimilarities.

4. Fig. 4 caption and Page 12: The authors introduce the terms LLC, OLC, and ELC. However, the range of lipid ratio and/or concentration as well as the rationale behind the assignment of these acronyms are not clear. They should clearly mention the range of each lipid concentrations that they denote as optimal, low, and excess.

5. Fig. 4A & C: It is interesting to note that the Sup35NM aggregation is non-nucleation dependent at both low and high lipid concentrations, however, at low, it appears to be much faster. Did the authors analyze the apparent rate constants? Also, can they rationalize why the observed trend in Fig. 4A (rate increases with an increase in DMPC concn) is in contrast to that observed in Fig. 4C (rate decreases as DMPC concn increases)?

6. Page 18: In the calcein release assay experiments, can the authors rationalize why do aggregates formed at an L/P ratio of 50:1 show an enhanced permeabilization efficiency compared to that at a ratio of 100:1?

7. In the discussion, the authors have mentioned the plausible formation of oligomeric aggregates. Did they find any evidence of the same from their FCS data?

8. A few acronyms such as DMPC, DMPS should be expanded. There are far too many typographical errors in the entire manuscript e.g. Kcal (should be kcal), Sup35NS, rH (subscript missing), 150 Mm, etc. including several journal names in the references.

06-Dec-2020

Dear Dr Chattopadhyay:

Manuscript ID: CB-ART-11-2020-000203
TITLE: Membrane composition and lipid to protein ratio modulate amyloid kinetics of yeast prion protein

Thank you for your submission to RSC Chemical Biology, published by the Royal Society of Chemistry. I sent your manuscript to reviewers and I have now received their reports which are copied below.

I have carefully evaluated your manuscript and the reviewers’ reports, and the reports indicate that major revisions are necessary. I also read your manuscript, and raised a few questions. I am not convinced by the authors' claim that the mechanism of lipid-mediated aggregation of Sup35NM (which forms functional beneficial amyloids for yeast) can be correlated with that of the human prion protein that forms toxic amyloids and is detrimental to humans. The claim appears far-fetched. Please address this issue along with other reviewers' comments

Please submit a revised manuscript which addresses all of the reviewers’ comments. Further peer review of your revised manuscript may be needed. When you submit your revised manuscript please include a point by point response to the reviewers’ comments and highlight the changes you have made. Full details of the files you need to submit are listed at the end of this email.

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Please note: to support increased transparency, RSC Chemical Biology offers authors the option of transparent peer review. If authors choose this option, the reviewers’ comments, authors’ response and editor’s decision letter for all versions of the manuscript are published alongside the article. Reviewers remain anonymous unless they choose to sign their report. We will ask you to confirm whether you would like to take up this option at the revision stages.

I look forward to receiving your revised manuscript.

Yours sincerely,
Prof Seung Bum Park

Associate Editor, RSC Chemical Biology

************

Reviewer 1

The authors have addressed all my concerns satisfactorily and improved the manuscript. I think the manuscript is now suitable for acceptance for publication.

Reviewer 2

The revised manuscript by Bandyopadhyay et al. addresses most of the concerns raised by the reviewers. Although the authors justify their choice of using Sup35NM for this study, the rationale that the mechanism of lipid-mediated aggregation of Sup35NM (which forms functional beneficial amyloids for yeast) can be correlated with that of the human prion protein that forms toxic amyloids and is detrimental to humans still seems unconvincing.

To
Professor Seung Bum Park
Associate Editor
RSC Chemical Biology

Dear Professor Park,
Thank you very much for your email (Dec 07, 2020) regarding the decision on our manuscript (CB-ART-11-2020-000203).
We are grateful that you have given us an option to resubmit a modified manuscript. We have carefully considered the comments of the reviewers and prepared this version of the manuscript, which addresses all of their concerns.
I sincerely hope that you will find the modified version of the manuscript suitable for publication in RSC Chemical Biology.
A point by point response of the reviewers’ comments have been provided below. We are also submitting a copy of the manuscript, in which all changes are highlighted.
Best regards
Krishnananda Chattopadhyay, PhD, FRSc
Head, Structural Biology and Bioinformatics Division
CSIR-Indian Institute of Chemical Biology
Kolkata, INDIA






Referee: 1
Comments to the Author:
The authors have addressed all my concerns satisfactorily and improved the manuscript. I think the manuscript is now suitable for acceptance for publication.
Response: We are grateful and thank the referee.

Referee: 2
Comments to the Author:
The revised manuscript by Bandyopadhyay et al. addresses most of the concerns raised by the reviewers. Although the authors justify their choice of using Sup35NM for this study, the rationale that the mechanism of lipid-mediated aggregation of Sup35NM (which forms functional beneficial amyloids for yeast) can be correlated with that of the human prion protein that forms toxic amyloids and is detrimental to humans still seems unconvincing.
Response: We thank the referee for giving us an opportunity to elucidate this concern in detail. It is well known that prion disease or transmissible spongiform encephalopathy is an infectious amyloid disease1. Human forms of prion diseases include Creutzfeldt-Jakob disease, Gerstmann-straussler-scheinker disease and fatal familial insomnia 2-4. The most common animal form of Prion disease is bovine spongiform encephalopathy or ‘mad cow’ disease, which is transmissible to humans 5. It has been hypothesized that a conformational change in prion protein (PrPC) into another form (PrPSC) makes the protein amyloidogenic, which then aggregates leading to the propagation of the disease 6.
There are several prion-like proteins, which exist in different fungi including yeast 7. Some studies suggest that aggregation of Sup35 prion protein may form functional beneficial amyloids for yeast since interaction of prions causes heritable traits8. Although, these yeast prion proteins are not infectious to humans, they carry the same transmissible phenotype as human prion protein. With human prions, an infectious disease propagates through a self-sustaining modification in the structure of a normal protein within the cell, seemingly without the help of any nucleic acid 9. With yeast prions, a similar mechanism yields a new heritable metabolic state, seemingly without a change in any nucleic acid. In addition, the yeast Sup35 protein contains a human prion-like domain 10. A conformation changes similar to human prion protein between the PrPC and PrPSC form has been found also with Sup35 and the proposed mechanism of the propagation of Sup35 aggregation has been found to be identical to that of mammalian prion protein11, 12. Hence, Sup35 has been used extensively and widely as a model protein to study the mechanism of the prion disease 10.
Human prion proteins are sometimes found to be associated with lipid membranes13-16. It is well acknowledged that lipids/membranes induce the aggregation of human prion proteins14. Whatley et al have shown that the vacuolation in nerve cells is drastically increased during prion aggregation, which further emphasizes the effect of membrane environments towards the aggregation of prion protein17. Fei wang et al, have found earlier that the PrP-lipid interaction can be initiated by electrostatics, which can be followed by hydrophobic interactions18. They show that the protein-lipid interaction can convert full-length R-helix-rich PrP to a PrPSc-like conformation under physiological conditions, supporting the relevance of lipid-induced PrP conformational change to in-vivo PrP conversion. Ganusova et al. and Chernova et al. have shown that lipids/membranes play a role in the aggregation of Sup35 inside yeast cells19 20. It has been shown by various research groups that Sup35 may propagate as a prion in mammalian cells and that GPI anchoring facilitates aggregate propagation between N2a cells, resembling mammalian prion behaviour21-24.
Since the proposed mechanism of the propagation of Sup35 aggregation was found similar to that of mammalian prion protein, Sup35 has been used extensively and widely as a model protein to study the mechanism of the prion disease. It may be noted that this manuscript does not explore the mechanism of toxicity (or the beneficial effect) in yeast, which would depend on multiple factors, the understanding of which is beyond the scope of the present manuscript. We have carried out some toxicity experiments in mammalian cells (not in yeast) only to understand how these lipid bound aggregates (as a mimic of their human prion counterpart) induces toxicity in mammalian cells and these experiments should not be used as a viable measure of in vivo toxicity in yeast.
To address this concern, we have modified the introduction part of the manuscript suitably and indicated that the predominant aim of this paper to use this protein as a model system for the understanding of the lipid induced aggregation. We strongly believe that the mechanism of lipid-mediated aggregation of Sup35NM shown and described by this present study can be convincingly correlated with that of the human prion protein. We note that one sentence in abstract ‘The toxicity of the aggregates formed within OLC range was found to be greater’ may be misleading and hence we deleted that sentence (highlighted in the abstract portion). We have also modified several portions of the Results, Discussions and Conclusions portions suitably to emphasize that the toxicity measurements have been carried out in mammalian neuroblastoma cells (please refer to the highlighted portions).




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3. K. Hsiao, S. R. Dlouhy, M. R. Farlow, C. Cass, M. Da Costa, P. M. Conneally, M. Hodes, B. Ghetti and S. B. Prusiner, Nature genetics, 1992, 1, 68.
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6. N. J. Cobb, F. D. Sönnichsen, H. Mchaourab and W. K. Surewicz, Proceedings of the National Academy of Sciences, 2007, 104, 18946-18951.
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9. G. C. Telling, M. Scott, J. Mastrianni, R. Gabizon, M. Torchia, F. E. Cohen, S. J. DeArmond and S. B. Prusiner, Cell, 1995, 83, 79-90.
10. J. R. Glover, A. S. Kowal, E. C. Schirmer, M. M. Patino, J.-J. Liu and S. Lindquist, Cell, 1997, 89, 811-819.
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15-Jan-2021

Dear Dr Chattopadhyay:

Manuscript ID: CB-ART-11-2020-000203.R1
TITLE: Membrane composition and lipid to protein ratio modulate amyloid kinetics of yeast prion protein

Thank you for submitting your revised manuscript to RSC Chemical Biology. After considering the changes you have made, I am pleased to accept your manuscript for publication in its current form. I have copied any final comments from the reviewer(s) below.

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Prof Seung Bum Park

Associate Editor, RSC Chemical Biology
Professor, Chemistry Department, Seoul National University, Korea

Reviewer 1

Authors have improved the manuscript further by editing the parts of introduction, results and discussion pitching a better physiological context. I think the manuscript is now certainly in a shape to be accepted by RSC Chemical Biology.