On 2021-06-27 04:11:33, user Mel Symeonides wrote:

With this study, Patterson et al. present a potentially very significant finding: that SARS-CoV-2 antigen persists in non-classical monocytes from Long COVID patients up to 15 months after the initial infection. The data supporting this finding are of moderate to low strength, as presented, primarily due to a wide range of major and minor presentation issues that are listed below. Most of these can be addressed easily, though it is unclear if some additional controls may be required. Finally, some orthogonal approaches are suggested that could be potentially very valuable in terms of increasing confidence in the findings (namely microscopy and immunoblotting), though these are not essential for the interpretation of the results as shown.

The authors are to be commended for tackling Long COVID head-on and getting right to the heart of the matter in terms of finding the pathological cause of this disease. That said, unfortunately, this manuscript requires considerable revision in order to be interpretable and allow others to reproduce the findings (which will be of critical importance, given their potential significance).

Major issues:

• Table 1 and the accompanying text seems to indicate that PBMCs were tested for the presence of viral RNA by ddPCR. However, in the Material/Methods section, it is stated that nucleic acids were extracted from plasma, not from PBMCs. Please clarify this point as it is of critical relevance. Indeed, both plasma and PBMCs should have been individually tested in order to determine whether viral RNA was solely intracellular.

• It is very unclear what Figure 2 is presenting. Presumably each row represents a different subject, but it is not denoted which subject belongs to which group, making intepretation very difficult. I presume this was an ommission.

• Supplementary Table 1 was not provided, making it very difficult to evaluate the flow cytometry data. Even if that table were present, the methods provided for flow cytometry are very sparse. What steps were undertaken to establish the specificity of the Spike antibody? Was the Spike staining done after fixation and permeabilization? Was PE conjugation of this antibody done in-house, and if so, using which kit, and how was it verified that the conjugation and quenching were successful and that staining was specific within the context of the entire antibody panel? Were FMO controls done in the context of this new panel that includes the S1 antibody? Was Fc block included? etc.

• In general, the Figure Legends are very sparse and should be much more descriptive.

Minor/moderate issues:

• Table 1 shows that one of the study subjects was asymptomatic. Where is this subject grouped in the subsequent analysis? ALso, "NS" is not defined, presumably it means "nasopharyngeal swab"?

• In Figure 2, left column, the CD14/CD16 gates shown were not applied equally from sample to sample. Furthermore, in the middle column it looks like S1+ non-classical cells tend to have a low-SSC profile, while S1- cells have a high-SSC profile that clusters together with intermediate cells. This suggests that the intermediate/non-classical discriminating gates may not have been set appropriately.

• The quantification shown in the middle column of Figure 2 is labeled "CD16+CD14+COVIDS1+", however no "CD16+CD14+" subset is defined. Presumably the authors refer to the aggregate of the "CD14++CD16+" intermediate and "CD14loCD16+" non-classical subsets. This should be clearly stated as it makes interpretation of the data shown very difficult. Additionally, the quantification is based on the aggregate population, whereas based on the color coding, one would expect individual quantification for each subset. Given the relatively very minor contribution of the intermediate subset to the observed Spike S1 signal, it is unclear why this was included at all in this plot - why not just show the non-classical subset and base the quantification solely based on that, or alternatively, show quantification of each subset rather than their aggregate?

• The labeling in Figure 3 could be better, the angled X axis labels are very difficult to follow. Maybe just indicate the monocyte subset as a title above each plot, and/or label each plot as a subfigure?

• No information is provided on the statistical analyses done.

• I did not look into all the cited work, but in one case (ref. no. 19) was puzzled to see that a review article was cited in which the relevant information was in turn derived from a single primary research article. Surely it makes more sense to just cite that primary research paper rather than the review?

General comments:

• Why was S1 the only SARS-CoV-2 antigen stained for? One would expect that you would have quickly tried to look for other viral antigens, particularly Nucleocapsid, in order to begin to understand whether there might be virus particles present, especially since you found viral RNA in some samples. Additionally, some microscopy data on sorted non-classical monocytes would have been very valuable to validate what you see by flow cytometry, also because one could then evaluate whether the Spike signal in these cells looks like the expected pattern for protein being actively synthesized by the cell and present on the cell surface, or whether it is captured antigen from some site of viral persistence and is sequestered in some intracellular compartment. Finally, a Western blot for Spike (and other viral antigens) in flow-sorted monocytes would be of immense value to further validate the presence of this antigen and observe the state of the protein - indeed, it is rather odd that you seemingly went for LCMS before trying either microscopy or a Western blot!

• The potential connections with the CX3CL1 pathway mentioned in Discussion are very interesting. Unfortunately, the authors have not demonstrated any elevation of CX3CL1 associated with severe acute COVID or long COVID disease, nor the presence of CX3CR1 on the particular cells of interest. If such data exist, please present them, otherwise this Discussion is rather speculative and much more work will be required to frame it in the appropriate context for a primary research paper. Alternatively, this discussion might be better suited for a separate Review article.

• Much of the published work on Long COVID and other post-COVID conditions such as MIS-C is omitted here, and should be cited and discussed as appropriate.

Mel Symeonides, Ph.D.<br /> Postdoctoral Associate<br /> Department of Microbiology & Molecular Genetics<br /> University of Vermont<br /> Burlington, VT

On 2021-06-26 22:40:59, user Sarah Elgin wrote:

It has been suggested by Jo Handelsman that it would be good to have 5-7 such centers for Research Engagement, distributed across the country, and we concur.

On 2021-06-26 15:16:11, user Raymond .Enke wrote:

I love the idea for a National Center for Science Engagement. Groundwork laid by the SEA-CUREs, DNA Barcoding, GEP, etc have proven that various CUREs can be implemented with a reasonable per student cost. Organization at the national level would only further decrease cost of implementation as the efficiency of implementing these CUREs increases. How do I get involved?

On 2021-06-26 20:46:44, user Stefano Vianello wrote:

Hello, I was looking for the list of VE and AVE markers you mention in the text but I could not find the Supplementary Tables you reference. I wanted to ask whether these will be uploaded on biorxiv too. Thank you!

On 2021-06-26 20:40:48, user Marco Salemi wrote:

There are several methodological problems with this paper. For example, the phylogeny reconstruction is over simplistic and does not include any test to evaluate the statistical robustness of the conclusions. However, the critical flaw is the lack of sufficient phylogenetic signal in the sequence data that unavoidably results in the uncertainty of the root of the SARS-CoV-2 phylogeny. As discussed by Mavian et al. (PNAS 117, 23, 12522-12523, 2020) and later confirmed by other studies, early SARS-CoV-2 sequences from China (and even Europe and USA) displayed (as expected for a pathogen recently introduced in a new species) a high degree of genetic similarity resulting in statistically poor phylogenetic signal. This means, in essence, that the number and distribution of polymorphic sites in the sequences, which are used to infer a phylogeny (no matter what algorithm is used), is not sufficient to decide with a high degree of confidence among alternative evolutionary scenarios (i.e. topology of the phylogenetic tree, exact position of the root). The new "recovered" consensus sequences in the tree (even assuming that they are completely reliable) do not add any significant phylogenetic signal to the data (this can be easily proven with a simple likelihood mapping analysis). So, if anything, the recovered deep sequence data sheds exactly the same uncertain light on the early Wuhan SARS-CoV-2 epidemic as all the other sequences known so far.

On 2021-06-26 12:03:13, user Nicolò Cavalli wrote:

Thank you professor Bloom for your impressively clever and incredibly important work.

On 2021-06-23 07:38:24, user Alex Crits-Christoph wrote:

This work by Professor Jesse Bloom details a phylogenetic analysis of a set of SARS-CoV-2 genomic sequences originally submitted to the Sequence Read Archive, likely by the authors of Wang et al. 2020, in February - March, 2020. Both a preprint, and a later paper (by Wang et al.), were publicly available describing these sequences, including key aspects of their genomic features. However, independently of the preprint or paper, which make no direct reference to an NCBI submission, the sequences been marked for deletion on NCBI, but were re-obtained by Bloom via internet backups of the data. While sharing more genomic data from the early epidemic can be valuable, I believe the current version of this work makes several errors that are important to address in both scientific content and critically, in scientific communication.

In general, the work is vague or remiss about extremely important context and details about the sequences in question. To begin, the genomes obtained are consistently referred throughout the title and abstract (and indeed most of the text) as being from the "early" epidemic. This terminology is too vague, as it may invite the reader to assume that the genomes include the earliest cases known - in fact, they are not, and were originally reported by Wang et al. 2020 to be from January 2020. Over 25 genomes had previously been obtained during 2019 for SARS-CoV-2. To properly interpret the context of this work, an emphasis on the timing is critical and should not be avoided in the abstract or title.

Secondly, the abstract and title both strongly give the inaccurate impression that the re-obtained sequences alone newly demonstrate that the known and reported genetic diversity of viruses in the Huanan market was not representative of all circulating SARS-CoV-2 variants at the time. This is alluded to in the title, which says they "shed more light" on the early epidemic. Yet, this is not supported by the data in the manuscript: it was already known that the genetic diversity of viruses obtained from Huanan market cases was not representative of all genetic variants circulating at that time. As can be seen most clearly in Figs 3 and 5, the new sequences obtained were not completely unique in sequence or unusual in case timing. There were already several reported publicly available similar genomes with for the most part identical sequences from the early epidemic. The author is certainly aware of this, as it is evident from the data presented and from the works cited (both Garry 2021 and Kumar et al. 2021 discuss this at length), but this key point is not emphasized in the title or abstract, and indeed is a weakness of the importance of the work itself.

Thirdly, in the introduction the work makes several key omissions about the timing of cases. The introduction directly suggests that the Huanan market is unlikely to be a site of zoonosis because a number of early cases could not be confirmed to be connected to the market; However, this was true of SARS-CoV-1 in Fushan as well. The author also neglects to mention that a significant fraction of cases were connected to *other* markets in the city, including the earliest cases (as described in the WHO report). And indeed, if there were multiple spillover events, e.g. from a shared wildlife supply chain that connected multiple markets throughout the city, even with perfect contact tracing data one would not expect all cases to be connected to one market.

Fourthly, I believe the inclusion of Figure 2 in this paper is highly unprofessional and misleading. This is a screenshot of an email from a scientist who is not associated with the papers or data described in the data; indeed, the only relevance between them seems to be a shared nationality of the author(s). Additionally, as of June 2021 the data described as 'deleted' in this screenshot is publicly available again on NCBI. While I understand that Bloom likely did not realize this mistake, it is difficult to justify the inclusion of this figure in a scientific work.

Fifthly, and perhaps most importantly, I think the previous point happens to provide a fortuitous lesson about a key error that Bloom makes in assuming misconduct on the part of the Wang et al. 2020 authors. He writes "It therefore seems the sequences were deleted to obscure their existence". It is implicitly assumed that Bloom believed that to also be true of the data described in Figure 2 - hence its inclusion - but its recent re-publication on NCBI makes it abundantly clear that was not the case. To be honest, this is not surprising. Claims of scientific misconduct made from a distance, without knowledge of the details and circumstance surrounding the issue, have the potential to appear convincing despite having perfectly ordinary (or perhaps slightly less than ideal, but not nefarious) scientific rationale.

Similarly, there is also evidence that scientific misconduct is also highly unlikely to be the case with the dataset that is described in this paper. Primarily, this is because the paper describing these sequences was published in a journal several months later. If the authors were indeed trying to obscure their data, they would simply also not publish their paper in a public journal, or request it to not be published after submitting for review. If these sequences were removed for the purpose of obscurity, it is also worth noting that such an effort clearly flopped - because as described above, these sequences do not immediately provide any completely new knowledge about the genetic diversity of SARS-CoV-2 in the early pandemic. In both the preprint and the paper (the first submitted before data removal; the second published likely after), no mention of a BioProject accession is made, and instead it is said that the data is available upon reasonable request from the authors. If the writers initially intended for the data to be made public, standard practice would have included the BioProject reference (or even a placeholder) in the text. The fact that there was never such a reference makes it quite evident that there likely was a miscommunication between co-authors about whether the data was intended to be released to NCBI.

The reality is that minor scientific missteps and less-than-ideal circumstances surround the sharing of scientific data all of the time. The process of publishing on scientific data is fraught with tiny details and hard work, the trainees responsible for it are often overworked, and there are often unfortunate but relatively ordinary scientific incentives to avoid making as much data public as should be. The rationale behind what data is and is not shared for scientific works are often nuanced, and sometimes quite personal. The scientific process would be better if it were not the case, but these forces are almost universal, and everyone encounters them in scientific work. In this circumstance, like in the circumstance outlined in Figure 2 of this work, these ordinary forces of scientific circumstance are almost certainly more likely the case than direct censorship or misconduct. It is unfortunate and alarming that this work as it currently stands baselessly contributes to an environment where many readers assume the latter depending on the country of origin of the original authors.

Minor point:

At the bottom of page 5: "But although there are unusual aspects of RatG13's primary sequencing data". This statement is vague, the language is unscientific, and many interpretations of it would not be supported by the citations provided. I would recommend that Bloom change this sentence to present a coherent scientific statement if indeed there is a point about genome quality to be made there that is relevant to the text.

On 2021-06-25 07:46:16, user Jagan Mohan wrote:

It is a nice example of how a bacteroides that uses non-PUL encoded enzyme to grow on barley beta glucans

On 2021-06-25 07:14:32, user Anton Bosch wrote:

Fascinating finding! Makes sense perhaps from the perspective that women to score higher on the trait conscientiousness?<br /> I believe there may be a flaw/limitation in the statistical analyses that could be addressed:<br /> The gender results are nested within conferences, and so I wondered if a multilevel analyses is a more valid approach and could lead to different conclusions. The current statistical adjustments may not cut it. The issue that is raised here is comparable to the classroom problem: e.g. if in a study on academic aptitude one compares boys and girls, recruiting them from different schools/classrooms, then the results are nested within that. I.e., if classroom A has a much better teacher and 70% boys, and classroom B has a poor teacher and 70% girls, and there are no gender differences within classrooms, one may reach the flawed conclusion that on average girls are academically weaker. <br /> In same manner: some conferences (or chair persons) may have a more lax attitude towards time-keeping (or for whatever reason are less punctual). If those conferences (or chairs) happen to host more male speakers than that could account for the effect.

On 2021-06-24 23:24:06, user Nikolas Haass wrote:

Highlights:<br /> • MITF regulates phenotypic heterogeneity in a 3D tumor environment in melanoma.<br /> • MITF affects molecular processes involved in cell-ECM interaction.<br /> • Cell-ECM interaction mediates structural integrity and solid stress.<br /> • Phenotypic heterogeneity is controlled by solid stress via ROCK signaling.

On 2021-06-24 23:23:25, user Nikolas Haass wrote:

Significance: Phenotypic heterogeneity is a major culprit of cancer therapy failure. We demonstrate that phenotypic heterogeneity is controlled through tumor cell-ECM crosstalk resulting in altered tumor microarchitecture, mechanotransduction and Rho-ROCK-myosin signaling. Melanoma shares these physical properties with any solid cancer underscoring the importance of our findings for therapeutically targeting this phenomenon.

On 2021-06-24 18:28:36, user Marc Wein wrote:

This manuscript has now been published:<br /> https://elifesciences.org/a...

On 2021-06-24 09:39:28, user Max Telford wrote:

Hope ok to point out that (I think) the first use of the method of aligning codons to amino acids was in our paper https://doi.org/10.1073/pna....

On 2021-06-24 00:40:45, user Wenpeng Liu wrote:

amazing work, it is so interesting to see NSD that not dependent on fork reversal. Have you test if FBH1 co-depletion with LAMN can rescue the NSD? see this paper "Two replication fork remodeling pathways generate nuclease substrates for distinct fork protection factors"

On 2021-06-23 21:50:08, user Willson Gaul wrote:

This paper has now been published in the Bulletin of the British Myriapod and Isopod Group (2021) Volume 33. The published version is available at https://www.bmig.org.uk/sites/www.bmig.org.uk/files/bulletin/BullBMIG33-2021p52-62_Gaul-Tighe_C-sylvestre.pdf

On 2021-06-23 15:01:58, user Stefano wrote:

Really interesting preprint! May I ask for a clarification point? If I understood correctly, you are checking for divergence from the "demographic makeup of the scientists who publish their primary research in Nature" (and specifically, last authors). Yet it has been shown that this demographic (i.e. scientists that are published by Nature) is itself biased. E.g. Abdill 2020 10.7554/eLife.58496 showing that several Nature titles disproportionately publish research from the united states. It is also possible to imagine bias towards Western authors given Nature's publishing model/fees etc.. Doesn't this suggest that the biases in Nature journalism, with respect to global science, are likely even stronger than what measured? I.e. Nature journalism over-represents English/men authors compared to a reference that already over-represents them, and underrepresents East-Asian/women authors compared to a reference that already under-represents them? I would be really interested in hearing your thoughts on this point.

On 2021-06-23 11:58:40, user Tom Jacobs wrote:

Interesting. I like the work. Just as you write, folks generally do not include the Cas- or gRNA/crRNA-only controls anymore. This was done back when CRISPR took off but it has largely been dropped.

I wonder about the sRNA sequencing. Did you observe the intact DR + spacer in the reads, or only the processed forms? It looks like your library prep protocol would have excluded larger fragments. You mention the reads are 21-24 nt in length, but which part of the DR+spacer does that contain? Is it a single species? Or spread out across the 28-nt spacer?

sRNAs should be produced along the entire length of your TRV vectors. Maybe what you are observing with the viral work is just the production of a functional siRNA from the viral RNA (standard VIGS) and not from a crRNA? Unless I missed it, all the results show that the presence of the crRNA vector is sufficient, but is there evidence that expression of the crRNA is required? I'm curious what would happen if you removed the U6 promoter and/or the DR. Or change the initiating nucleotide. That could establish that GIGS requires crRNA expression and not just presence.

On 2021-05-21 06:34:43, user phil_lefty wrote:

https://www.nature.com/arti...

We found complementary results with an RNA silencing effect without Cas13 in mosquito cell lines.

On 2021-06-23 10:16:32, user Andrea Degasperi wrote:

Congratulations for this wonderful work! May I just make sure that our approach implemented in the signature.tools.lib package is used correctly? From the supplementary notes you provide it seems that the guidance for using our method is not followed. We advise using at least 20 bootstraps with 200 repeats and filter of best runs with RTOL=0.001 (see “what parameters should I use for signature extraction”, https://github.com/Nik-Zain.... However, in the supplementary notes it is stated that 100 bootstraps with no filter is used. Also, the default parameters shown in our package, in particular repeats=10 is only meant for testing, not for practical purposes, as at least 100 repeats are in general necessary for small medium problems.

On 2021-06-22 23:53:26, user Maulik Patel wrote:

I am very proud to post this manuscript from my lab. It represents more than 3 years of work on a project initiated and executed by an extremely talented graduate student James Held in the lab. We would love to receive helpful feedback on the manuscript! Thank you.

On 2021-06-22 13:41:59, user Wenhu wrote:

Hope a drug based on this concept could eradicate malaria one day!!!

On 2021-06-22 04:41:27, user Hamid Gaikani wrote:

This preprint was peer-reviewed in "Frontiers in Fungal Biology" and is currently available under the title of "Systematic prediction of antifungal drug synergy by chemogenomic screening in Saccharomyces cerevisiae"<br /> doi: 10.3389/ffunb.2021.683414

On 2021-06-22 03:26:06, user Senjie Lin wrote:

That is exciting finding, offering support for the postulation that Symbiodiniaceae might use its miRNA to influence coral host's gene expression (DOI: 10.1126/science.aad0408). Looks like a perfect example of adaptive co-evolution.

On 2021-06-22 00:48:55, user Guest wrote:

Have the sequencing reads been deposited to a public repository?

On 2021-06-22 00:20:06, user Jingsong Zhang wrote:

The new version of this preprint is available at https://www.nature.com/arti...

On 2021-06-21 23:37:46, user Sue Biggins wrote:

We would love feedback on this manuscript, ideally by mid-July #FeedbackASAP

On 2021-06-21 16:36:33, user Philip Cook wrote:

Now published in Nature Methods:

https://www.nature.com/arti...

On 2021-06-21 08:33:48, user Benjamin S. Simpson wrote:

Fascinating stuff, a great paper. May I ask, in the full paper do you plan on releasing the full list of scaling and non-scaling genes as supplementary? I have a few areas I would love to check. I am sure there are many who would do the same.

On 2021-06-18 00:21:09, user Daniel Ricardo Matute wrote:

Data and scripts: https://github.com/adagilis...

On 2021-06-16 14:01:01, user Marc RobinsonRechavi wrote:

Under Data Availability, the authors write:

All scripts/data used for analyses and to generate plots are available on request, and will be made available on Dryad prior to publication.

This is a publication, i.e. it is made public as part of the scientific record and is citable, thus I strongly invite the authors to make the corresponding scripts and data available without delay.

On 2021-06-17 21:05:43, user Huanglab wrote:

Final version has been published https://www.mdpi.com/1422-0...

On 2021-06-17 21:04:42, user Huanglab wrote:

Final version has been published on J Med Chem. https://pubs.acs.org/doi/pd...

On 2021-06-17 15:57:46, user Abraham Smith wrote:

For users without a suitable GPU, a tutorial is now available for installing and running the RootPainter server with Google Colab:

https://colab.research.goog...

The tutorial also includes extra instructions on how to get started with annotation and using the client software.

On 2021-06-16 05:58:43, user Roeland KINDT wrote:

The article has been published now in PeerJ:

Kindt R. 2021. AlleleShift: an R package to predict and visualize population-level changes in allele frequencies in response to climate change. PeerJ 9:e11534 https://doi.org/10.7717/pee...

On 2021-06-16 03:10:21, user Joy Kim wrote:

This manuscript is now accepted for publication in Journal of Cell Science, under the revised title of "Spc1 regulates the signal peptidase-mediated processing of membrane proteins".

On 2021-06-15 23:57:01, user Alejandro Heuck wrote:

Some comments that may help the authors

1) Fig. 2b, what cells are shown in this figure? The legend mentioned MEFs Vim+/+ and Vim-/-, but it is not indicated in the panel,

2) Fig. 5g. The authors claim that based on the reduced hemoglobin release observed for Q308P (40%) the “pore formed by IpaC Q308P is partially closed” . If the mechanism of RBC lysis is osmotic lysis, a pore large enough to allow water to go through will trigger RBC lysis. The overall hemoglobin release reflect the number of RBC with at least one pore, it would not be directly related to the size of the formed pores as suggested.

3) Interaction of IpaC with intermediate filaments (IFs) was tested in solution (yeast cytosol) (Nat. Microb. 2016), where IpaC does not adopt its native membrane-inserted conformation (as in translocon pores). While those experiments suggested a potential interaction between IpaC and IFs, there are not data showing a direct interaction between IpaC and the IFs in functional translocons. While This is very difficult to show, but one should be careful when using this assumption (or model) to interpret new experiments.

4) The authors claim that "actin polymerization induces conformational changes to the T3SS translocon pore" . However, it is the inhibition of actin polymerization by CytD that affects the proper assembly of the translocon in the target cell membrane. In the absence of CytD, the translocon assembles properly and actin is polymerized.

5) check lines 251-252 for number of mutants and repeated ones

6) line 382 was E. coli induced with IPTG?

7) line 387, what was the ratio RBC/bacteria used during the hemolysis assay?

8) line 415, did the authors consider the possibility of separating detergent resistant membranes containing translocators in the pellet under this experimental conditions?

9) line 430, labeling should be insertion

10) line 436 define F buffer

On 2021-06-15 23:54:35, user Mohammad Dehghani Ashkezari wrote:

This article is now published on Limnology and Oceanography Methods:

https://doi.org/10.1002/lom...

On 2021-06-15 17:31:55, user Paul Herron wrote:

Super story and delighted to hear that it's not just actinobacteria from the G+ves that have linear replicons. Any idea how end-patching is carried out? Did you physically recover the telomeres? WGS doesn't go all the way to the replicon ends..... https://www.biorxiv.org/con...

On 2021-06-15 14:22:08, user NITIN NARWADE wrote:

Dear Authors,

Really wonderful study.

Is it possible to access the raw data OR processed scRNA-Seq count matrices for this study?

Thanks in advance!!

Regards,<br /> Nitin Narwade

On 2021-06-15 12:38:10, user Vinicius Waldow wrote:

Have you already submitted your work? I'm looking forward to the publication.

On 2021-06-15 11:04:54, user Iain Cheeseman wrote:

My co-authors and I welcome additional public comments on this work. Thanks! #FeedbackASAP

On 2021-06-14 23:28:24, user Fraser Lab wrote:

My co-authors and I welcome additional public comments on this work, ideally by the end of June, 2021! #FeedbackASAP

On 2021-06-14 19:49:18, user Staci Engle wrote:

Interesting findings! What time relative to the lights on/off do you administer MCH and GW803430? And how long after the last dose of MCH and GW803430 do you perfuse the mice?

On 2021-06-14 19:49:00, user Fraser Lab wrote:

EDITORIAL COMMENTS

Reviewers agree that this is an excellent showcase of state of the art native MS as applied to membrane proteins. The detection of a small drug bound in the complex with the membrane is an impressive technical achievement. There is some concern that these experiments may teach us more about the limitations of native MS than about AM2 function specifically; even in face of that concern, this manuscript is valuable. The key technical considerations that merit further caveats/discussion in the manuscript are:

1) contrasting how insertion into detergent/nanodisc vs. translation and incorporation into “real” membranes might affect the results

2) given differences in native mass spec and biases about certain oligomers flying, etc better - is there any orthogonal metric to use to calibrate how each oligomer might be biased or to calibrate the reproducibility<br /> - See especially this comment by Reviewer #3: The authors offer two interpretations of their data in the discussion: 1) that it is very challenging to capture the pure tetramer 2) that the oligomeric states of AM2 are more complex than previously thought. The former is unlikely to have any physiological relevance while the latter could have important implications for development of novel therapeutics. A third interpretation could also be that the oligomeric profile observed is a byproduct of the native MS technique utilized. This manuscript would be much more impactful if this study included experiments to differentiate between these possibilities.

3) the concentration dependence (of AM2 and of detergents) of the results

James Fraser (UCSF)

Note: I solicited some reviews and am acting as an “editor” and authenticator of their expertise to preserve their anonymity. Happy to facilitate any interactions between authors, reviewers, or any other interested party.

REVIEWER #1

In this study, Townsend and colleagues utilize native-state mass spectrometry to characterize the oligomeric state distribution of matrix protein 2 from influenza A (AM2) in response to varying environmental conditions and pharmacologic agents. AM2 is a well characterized viroporin, which are small transmembrane proteins which oligomerize into ion-conducting channels during viral infection. Viroporins are clinically validated drug targets, and investigating the structural and mechanistic properties of viroporins is important for understanding their roles in the viral replication cycle and could aid future drug discovery.

Most prior structural insights into AM2 have been obtained by X-ray crystallography or NMR. This manuscript adds to this structural investigation of AM2 by using native-state MS to investigate AM2 oligomeric states in the solution state and in nanodiscs, which could better reflect the physiologic membrane context. Their key findings are that 1) AM2 adopts a range of oligomeric states (monomers to hexamers) and 2) the distribution of these oligomers vary depending on environmental conditions (lipid composition, pH), small-molecule inhibitors, and mutations. The relative quantification of AM2 oligomer polydispersity is uniquely enabled by the authors’ use of native-state MS. This contrasts with the predominantly tetrameric state that has been appreciated from prior structural studies of AM2. The authors’ findings present a compelling case for investigators to employ careful experimental design and data interpretation when working on AM2/viroporins and other dynamic and oligomeric proteins. The implications of this polydispersity on AM2 function and viral replication remain unknown. Insights into the energetics and dynamics of interconversion of these oligomers, and application to other viroporin homologs are also areas for future investigation.

The manuscript is written clearly and the researcher’s rationale and methods are described in detail. Specific comments are listed below:

How were the equilibration time and temperature of the samples for native-state MS analysis chosen? These two parameters (among others) can have significant effects on the population distribution of oligomers observed.

Page 5, first paragraph. “The precise oligomeric state distribution varied substantially between replicate measurements, indicating variable and relatively nonspecific oligomerization.”.

Could the authors provide some context/examples on this variation between replicates? For most figures, a representative spectra or an average with error bars (with no individual data points noted) are presented.

Could the authors comment what implications the observed replicate variability would have on their interpretations of AM2 polydispersity?

Could the authors explain why they conclude that the oligomerization is driven by relatively non-specific interactions? Prior structures of AM2, at least of the tetramer, show a symmetric oligomer with specific contacts being made at the interface between the monomers to form a conducting pore. Would the authors expect the interactions in the non-tetrameric states to be similar to or different from those observed in the tetramer?

Were oligomers/aggregates larger than hexamers observed?

In Figure 4, the distribution with 0 uM AMT of WT AM2 solubilized in C8E4 appears quite different than in Figure S1 and in the Figure S9 QToF data. Could the authors comment on the reproducibility of these distributions?

Monomeric AM2 appears to be very low or non-existent in detergent, but is present in nanodiscs. Could the authors comment on how the detergent vs nanodisc environment could be responsible for the observed differences?

Did the authors investigate the dependence on the AM2 to nanodisc ratio on the oligomeric distribution of AM2?

The authors suggest that the S31N mutant is unable to bind amantadine because it is locked in a predominantly non-binding pentameric state (based on Figure 4 data). However, in nanodiscs, the S31N mutant forms monomers/dimers/trimers but no larger oligomers. Could the authors comment on this observed difference in their data, and how the authors’ proposed mechanism of resistance relates to previous studies on the mechanism of the S31N mutant?

Page 9: “Importantly, AM2 S31N nanodiscs did not show any mass defect shifts upon addition of amantadine, confirming specificity of drug binding.” Could the authors include this data, potentially in the supplementary file?

REVIEWER #2

The paper by the Marty group investigates by native MS of nanodiscs the oligomerization state and drug binding properties of the viral Matrix protein 2 from influenza A (AM2) at different chemical environments. Interestingly, AM2, which is thought to exist primarily as a tetramer, is shown in this study to be highly sensitive to the chemical environment and displays a distribution of assembly states, depending on pH and lipid composition. The findings that illuminate the polydispersity of Am2 provide new potential mechanisms of influenza physiology and pathology. The data is high quality and reproducible and the manuscript is well-written. I recommend addressing the points raised below.

1) According to the materials and methods section, the protein was analyzed at a concentration of 50 μM (of the monomer?), which is quite high. Understandably, if a tetramer is expected, then higher amounts of the monomer are needed. However, since the protein appears in a range of assembly states, non-specific oligomerization should be ruled out.

2) In the few cases in which dilution experiments were performed the extent of dilution is not indicated, i.e. what are the starting and end concentrations.

3) The data in Figs. 4, S1-S6 and S9 is processed, can the authors provide representative raw spectra, so the quality of data can be estimated.

4) The discussion section should be extended, with emphasis on the biological relevance of the results. Like what is the composition of the natural host membrane? How can polydispersity in assembly states benefit the influenza virus? and their similarity to the membranes tested. Does any of the tested conditions mimic the natural environment of the host membranes? Can any conclusions be drawn as to the endogenous assembly state of AM2 in the host cells? In a structural and chemical point of view what is the mechanism in which pH or lipid content affect assembly?

5) AM2 is post-translationally modified. Can the author comment on this aspect and how do they think it affects the assembly state distribution?

6) In Figs 4, S1, S2 and S3 the concentration of Am2 is not indicated.

7) The mass defect analysis should be explained.

8) Raw data of the IM-MS results shown in Fig. S6 should be provided.

9) Theoretical and measured masses, including mass measurement errors should be added (also of drug binding). Perhaps in a table.<br /> 10) Figure 2, in panels E and F the y axis in the inset is distorted.

11) What does the cartoon in figure 5 demonstrate?

REVIEWER #3

In Townsend et al. the authors utilized native mass spectrometry to characterize the oligomerization state of the influenza A M2 channel in different environments and found that in contrast to what has been previously reported, AM2 exists in multiple oligomeric states depending on pH, lipid composition, and presence of drug. Of note, this study utilizes native MS to measure drug binding to a membrane protein in an intact lipid bilayer, which is technically challenging. Although this is a novel application of native mass spectrometry, additional experiments are needed to provide convincing data that would support the main conclusion, namely that the oligomeric state of AM2 is actually more polydisperse than previously reported. This manuscript would be greatly improved by addressing the following questions:

Major points:

1.The authors offer two interpretations of their data in the discussion: 1) that it is very challenging to capture the pure tetramer 2) that the oligomeric states of AM2 are more complex than previously thought. The former is unlikely to have any physiological relevance while the latter could have important implications for development of novel therapeutics. A third interpretation could also be that the oligomeric profile observed is a byproduct of the native MS technique utilized. This manuscript would be much more impactful if this study included experiments to differentiate between these possibilities.

1. The author's note that "There are several dozen X-ray or NMR structures of the AM2 TM domain in a variety of membrane mimetics, all depicting monodisperse homotetramers" yet most of their conditions do not replicate this finding. Could the authors please comment in more detail on how their conditions differ from the previously reported structural studies which indicate AM2 is present as a homotetramer? The authors mention that most studies used high concentrations of drug - are there other explanations as to why they observed high variability and complex instability where others did not? Do all the previous studies use drug to stabilize the complex? In cases where they did not use drug, what was different?

2. The fact that the replicate measurements showed significant variation suggests that these results may be due to technical complications rather than truly reflecting distinct complex formation. Did the authors consider using a positive control - perhaps something else known to form a tetrameric complex of similar molecular weight for comparison? This would help build confidence that utilizing native MS for this application can provide reliable data.

3. In figure 2 and S1, please provide intensity values associated with each condition. Larger complexes are harder to ionize and more likely to inadvertently dissociate in the gas phase. It is impossible to understand how well AM2 ionized in each of these conditions when it is presented as a percent of total. Have the authors considered creating covalently bonded versions of dimer, trimer, and tetramer AM2 to use as standards to accurately quantify the amount of each complex in each condition?

4. In figure S2, as protein concentration increases, a shift towards higher molecular weight complexes is observed. Is it possible this is due to protein aggregation and unlikely to be observed in physiological conditions?

5. The "orthogonal measurements confirm oligomeric sensitivity" section is confusing. What do the authors mean by oligomeric sensitivity? It is also unclear how the SEC data supports the authors' claims about the oligomeric state of AM2.

6. Please explain the statement "very small signals for bound drug were observed". Does this refer to the signal from AM2 or from the drug itself or for drug bound to AM2?

Minor:

1. Could the authors please comment on why the select conditions were chosen for figure 2? Supplemental figure 1 is more informative and is worth including in the main figures. Similar question for the other figures where parital datasets are shown in the main text.

2. Please clarify the concentration of AM2 used in Figures 1, 2, 3, 4 and S1 and S3.

3. Clarify which detergent was used in figure S9.

REVIEWER #4

The authors of this manuscript explore the effects of detergents, drugs, pH, and lipids on the oligomerization state of a well-studied viroporin from the influenza A virus, the M2 channel. Using native mass spectrometry as their main approach, the authors show that pH and the chemical nature of the membrane or membrane mimetic influence the observed polydispersity of M2. While native mass spectrometry captures a distribution of oligomeric states that was not seen in previous analytical studies, the question, ultimately, is whether this polydispersity is physiologically relevant or whether it highlights the need for rigorous testing and vetting of membrane mimetics for structural and functional studies.<br /> In the initial detergent study, the authors investigate how various detergents affect oligomerization of the channel at different pH. They show that certain detergents favor different oligomeric states over others and capture an array of states in the detergents tested. They then show that the binding of drug to the WT shifts the observed population distribution to favor the tetramer. They repeat these experiments with the S31N mutant, which forms pentameric assemblies in the given conditions.<br /> To see the effects of lipid bilayers on the oligomerization state of M2, they assembled M2-incorporated nanodiscs. They show that choice of lipid composition of the nanodiscs is crucial to the observed distribution of states with DPPC being the lipid that favors the homotetramer. Moreover, they show that they are able to detect mass defect shifts from drug binding, corroborating earlier work in the field. The authors repeat the nanodisc studies with the S31N mutant. From their lipid studies with and without drug, they again rationalize that the drug-resistance of the mutant to amantadine and rimantidine may arise from the formation of small oligomers that preclude binding.<br /> The big question is whether these newly observed states are physiologically relevant or whether they’re an artifact of the physicochemical nature of the local environment. Overall, the authors clearly show that the assembly of M2 is sensitive to its chemical environment, and from their data, seem to suggest that the observed polydispersity reflects the true distribution of states in the physiological context. The data showing the polydispersity is very convincing and serve as a reminder that the choice in membrane mimetics plays a critical role in determining which oligomeric state, whether functional or otherwise, is favored. However, if the point is that these non-tetrameric states have some biological or channel function, then the authors bear the burden of proof.

Major Comments:

• Why are the lipid nanodisc experiments only done at pH 7.4 and not other pH? In the detergent study, we clearly see a change in the oligomerization state brought on by a change in pH, and the authors speculate that the change in pH in the endosome could change the oligomerization state to higher order oligomers, so why is there no pH-dependent study of M2 in nanodiscs?

• There have been several studies that look at the effects of a completely different set of detergents on the conformational landscape of the channel using solution NMR (Thomaston et al. JACS 2019) or different lipids using solid state NMR (Mandala et al. JMB, 2017): how does this study compare to these results? If the authors do the detergent study with solution state NMR, would they see evidence for polydispersity? Similarly, if the authors do these same native MS experiments using the detergents and/or lipids discussed in these two manuscripts, would they see polydispersity or do these conditions favor the exclusive formation of the homotetramer? The choices for lipids/detergents are orthogonal to what has been published in the literature, so a couple of experiments with the same sample conditions (i.e. lipid/detergent and pH) would be insightful as to whether the previous conditions just happen to favor the homotetramer.

• In the amantadine-binding study of the WT and S31N in detergent micelles, the authors noted no major changes to the oligomeric state distribution for the mutant and conclude that the absence of a shift is indicative of lack of drug binding. They also suggest that the known drug resistance of the S31N variant arises because this mutant is locked into a novel pentameric state that is impervious to drug-binding. While this is an interesting hypothesis, their MS data does not prove that the drug is not binding. Moreover, they note that even in their WT samples, which show clear shifts, there is a lack of signal from the bound drug in their MS results, so how can the authors make the claim that S31N is not binding the drug? A similar comment can be made about the S31N nanodisc study, although the experimental evidence for drug-binding in the WT lends more support to this conclusion than the one made in the detergent study.

Minor Comments:<br /> - Can the authors rule out effects from the varying peptide:detergent ratios? Each of these samples was run at 2x CMC (seemingly standard in the native MS field) with a constant monomer concentration of 50 uM, which works out to very different peptide:detergent ratios. At the same peptide:detergent ratios, how do the distributions compare to each other?

• Since the higher order oligomers (i.e. hexamers) in LDAO seem stable, could they potentially crosslink these samples to get a low-resolution structure of the hexamer?

• Is there polydispersity evident in other detergents for S31N?

• Previous studies (Ref #35 in this manuscript, for example) which look at the oligomerization of M2 using analytical ultracentrifugation used dodecylphosphocholine (DPC) micelles as the membrane mimetic. Using this particular detergent, the authors of the JMB publication showed that the monomer-tetramer equilibrium was cooperative in the presence and absence of the drug amantadine. Is there a reason why DPC was not used in this study? It would be interesting to see what distribution of states this technique captures in the detergent primarily used for the classical analytical ultracentrifugation experiments.

• Can the authors comment on why the drug-binding studies were only done in C8E4 detergent? How does the drug affect the distributions of the oligomers in other detergents? Would the larger hexamer observed in LDAO also bind the drug?

• The authors comment that the thickness and fluidity of the membrane is known to modulate M2 activity and suggest that these changes are due to a shift in the observed population of states in their discussion. Functional studies (i.e. liposomal proton flux assays) in the various lipids tested would be helpful to drive this point home. I would like to see how the activity of M2 changes in these lipids and how it relates to the distribuition of states observed in the native MS.

• The authors commented on the bilayer thickness/saturation of DPPC as a potential reason for the tetrameric specificity of M2 in these conditions. Similar speculation into the chemical or physical properties of the detergents that give rise to the observed oligomeric distributions would be welcome.

• Figures

o Figure 2: Since the main take-home message from the figure is the deconvolved mass spectra, which clearly illustrate the polydispersity of the sample, it may help to flip the inset and the mass spectra or move the mass spectra to the supplemental. To someone who isn’t in the field of native MS, the representative mass spectra are distracting and detract from conclusions illustrated in the deconvolved spectra.

o Figure 3: A similar comment to the remarks made in Figure 2 can be made for this figure as well.

o Figure 5: Is there a reason for the exclusion of S31N data? Since the drug-binding can be clearly seen in the corresponding WT samples, it would be better to swap out one of the WT-AMT figures (since they both are very similar) for one that shows the S31N with the drug even if no clear mass defect shift is seen. The two concentrations of AMT binding to WT is probably meant to show

On 2021-06-14 17:22:34, user tracey ruhlman wrote:

A more recent, final version of this article has been published in The Plant Journal. The correct DOI: http://doi.org/10.1111/tpj....

Please contact TAR for pdf if desired. Thanks.

On 2021-06-14 16:19:56, user Alyssa Long wrote:

Hello colleagues and interested readers! During my "final" review of this manuscript, I noticed that I had copy-pasted a primer sequence incorrectly in the Methods section. The error occurs in line 168 of the currently posted preprint (I forgot to properly reverse-complement my reverse primer sequence). The correct sequence is 5'-TCCTCGGGTGTCTTAGCACT-3'.

On 2021-06-14 15:16:03, user Ariel Mundo wrote:

My co-authors and I welcome any comments or feedback on this work. Comments on the GitHub site where the code and data are shared are also appreciated!

On 2021-06-14 13:46:38, user Levi Waldron wrote:

This is interesting new work, but the statement that MultiAssayExperiment requires "loading the full dataset into the working memory, which precludes dealing with larger datasets" is not true. As a counter-example, the SingleCellMultiModal Bioconductor package represents the same 10x single-cell Multiome PBMC dataset using an HDF5 on-disk, out-of-memory representation with a DelayedMatrix interface, consuming 30.7 Mb of working memory (see example below). A better representation of MuData would as be a cross-platform representation that for Bioconductor users is likely compatible with the widely adopted API provided by MultiAssayExperiment.

Example:

library(SingleCellMultiModal)<br /> suppressMessages(scmm <- scMultiome(dry.run = FALSE))<br /> format(object.size(scmm), units="Mb")<br /> [1] "30.7 Mb"<br /> scmm<br /> A MultiAssayExperiment object of 2 listed<br /> experiments with user-defined names and respective classes.<br /> Containing an ExperimentList class object of length 2:<br /> [1] atac: SingleCellExperiment with 108344 rows and 10032 columns<br /> [2] rna: SingleCellExperiment with 36549 rows and 10032 columns<br /> Functionality:<br /> experiments() - obtain the ExperimentList instance<br /> colData() - the primary/phenotype DataFrame<br /> sampleMap() - the sample coordination DataFrame<br /> $, [, [[ - extract colData columns, subset, or experiment<br /> *Format() - convert into a long or wide DataFrame<br /> assays() - convert ExperimentList to a SimpleList of matrices<br /> exportClass() - save all data to files

On 2021-06-14 12:52:01, user Felix Grünberger wrote:

Unfortunately we could not upload the supplementary tables here. You can find them at https://github.com/felixgru....

On 2021-06-13 00:43:13, user Andreas wrote:

It seems obvious that an antigen directly introduced into the body would result in stronger AB level response than a substance that has to first overcome the bodies own passive and active defense mechanisms (epithelial layers), that also involve other peripheral antigen-protective mechanisms.

I see that the authors didn't stratify their data of the natural infected cohort for disease severity.<br /> It is obvious that a more severe disease would also result in stronger seropositivity (higher AB levels), although likely not approaching levels achieved by direct introduction of the antigen into the body.

Including just molecular test-positive and possibly mildly diseased and even asymptomatic subjects, not accounting for actual virus load, certainly will impact the overall seropositivity levels for RBP observed in natural infected subjects.

On 2021-06-11 20:51:51, user Maria Izabel Cavassim Alves wrote:

Thanks to Dr. Todd Jackman (Villanova), who emailed us a comment on our preprint, we have realized that there is an error in the distribution of TEX15 orthologs that we reconstructed: whereas we initially only detected the presence of a partial PRDM9 ortholog in Anolis carolinensis, there is in fact a complete TEX15 ortholog. As a result, the evidence for co-evolution of TEX15 and PRDM9 is less compelling (p-value = 0.058 in Table 1). We will be updating the preprint shortly to reflect this change.

On 2021-06-11 20:46:55, user Jessica Polka wrote:

My co-authors and I welcome additional public comments on this work, ideally by the end of June, 2021! #FeedbackASAP

On 2021-06-11 20:46:22, user Seyyed M Miri wrote:

No Conflict of interest.<br /> although some of the authors are working in private companies, there is no coflict of interest in this article. We recomment authors to declare it.

On 2021-06-11 06:48:20, user Shahid Jameel wrote:

The study is encouraging. However, every author has a conflict of interest and the competing interest statement is a misrepresentation of facts.

On 2021-06-11 01:06:47, user Sriharsha Talapaneni wrote:

For Figure 2, no WT shown which would be good for a reference. In 2C, it is unclear what is happening. A suggestion is to zoom out for a better image or do a zoomed out pic with a zoomed in figure beside it. Additionally, are both prox1a and tfa necessary? One subfigure could potentially be put in supplemental. Labels for arrows would also be helpful for 2D, F, and H. There also appears to be an inconsistency with dpf in the figure. Is the prox1a expression gone by 4 dpf? The reasoning for only showing 2 dpf might be needed. Concerning Figure 2F, a suggestion is to have a graph show foxa2 expression over time (1.5 dpf to 2.5 dpf). There also seems to be a resolution issue throughout the figure. A potential fix would be for 2F, to possibly trace it. To support claim and significance, we would also like to see more animals and different time points.

A potential future experiment could be the use of an organoid.

Moreover, I understand that the main idea of the paper is prove that zebrafish can be used as model system by conducting the experiments in various organ systems. But I believe that this point is kind of understand and people would normally get lost in the details of the figure and forget why you conducted experiments in different organ systems. Therefore, for this it would be better to mention and repeat it so that we understand the reason for the transition.

On 2021-06-02 02:43:23, user Emily Peng wrote:

Overall, the figures were very neat and sized appropriately. The staining was also well done.

For Figure 1, it would be more visually appealing if the bar graphs were bigger as the x-axis looked a little cluttered and cramped. Additionally, annotations for the images would be helpful. Some of the annotations were blurry and it was unclear where the fat staining was. Some potential additional figures could include overexpression. Additionally, Figures 1A-D seemed simple and could be put in supplementals. For Figure 3’s exploration of the gut, it would be helpful if the paper explained a little bit more on how this figure ties into the larger picture/hypothesis. It seemed kind of abrupt to show the enlarged lumen without a transition into how it relates to ApoB. With a more detailed explanation of the gut, this paper will be able to come full circle.

On 2021-06-01 18:11:46, user Mackenzie Fernandez wrote:

The staining for Figure 4 was very clear and well done, with the images sized appropriately.

Figure 4 has a helpful schematic, which could potentially be re-sized and made smaller. For 4B-G it might be helpful to include labeling which fish are represented. A suggestion is to maybe put corresponding 4B-G labels from the 4H and 4I bar graphs, or do some color coding.

For Figure 5H, it is unclear what the red staining is for. If it has stained the background, probably should not be there.

On 2021-06-10 20:03:55, user jgalaz wrote:

In your cryoET observations, how would you distinguish true, biologically-driven deviations from the hexagonal pattern vs disruptions due to mechanical forces during cryo preservation and/or artifacts from the missing wedge and/or errors in tilt series alignment during tomographic reconstruction?

On 2021-06-10 13:30:16, user Alessio Cantore wrote:

Congratulations, great work. I would suggest a bit more discussion around the inflammatory cytokine response that you observe following lentiviral vector (LV) administration. My understanding from the methods is that you use lab-grad non-purified LV, thus please consider that contaminants, such as plasmid DNA, host cell DNA, host cell protein, cell debris and potentially endotoxin may well account for the observed rise in some pro-inflammatory cytokines. Please also note that a single anti-histamine anti-inflammatory treatment (polaramine + dexamethasone) eliminated the hypotensive response observed in a single dog from our previous study and no such response has been observed in later studies in non-human primates. I would be happy to discuss further if needed. Good luck with your work. Best. Alessio Cantore, SR-Tiget, cantore.alessio@hsr.it

On 2021-06-10 09:34:35, user Marc RobinsonRechavi wrote:

Under Data availability, the authors write:

All underlying data and code will be persistently archived upon acceptance

This is a publication, i.e. it is made public as part of the scientific record and is citable, thus I strongly invite the authors to make the corresponding data and code available without delay.

On 2021-06-10 07:58:52, user Matt Springer wrote:

Erratum: In our paper's bioRxiv version and initiually published journal version, the graph in Figure 4 erroneously listed Y axis units as ng/dl instead of the correct ng/ml. The pdf for download at Tobacco Regulatory Science has been corrected. The authors regret the error.

On 2021-06-09 20:30:40, user Sven Laming wrote:

This article is now published in Frontiers in Marine Science: https://doi.org/10.3389/fma...

On 2021-06-09 02:14:15, user Daniel Cameron wrote:

Very catchy title and some quite interesting results. Xiaotong Yao suggested I raise my terminology concerns as a biorxiv comment:<br /> ‘Loose ends’ is a catchy title but I am concerned that the use of new terminology for existing concepts has the potential to confuse readers. The definition you are using for ‘loose ends’ is equivalent to concept of a single breakend variant defined in the VCFv4.1 specifications about a decade ago.

Whilst it is only recently that variant callers have actually explicitly reported VCF single breakends (GRIDSS2 from SR/OEA/breakend assemblies, PURPLE from unexplained CN transitions), the loose end/single breakend concept has a long history of implicit usage. For example, NovelSeq (Sahinalp, 2010) uses an orientation-constrained assembly approach (OEA+/OEA-) very similar to that of jabba to produce what this paper calls loose end assemblies (although what NovelSeq does afterwards is different). The assembly similarity can also be seen in GRIDSS1 which uses the terms ‘breakend assembly’ and ‘anchoring reads’ when discussing it’s separate assemblies of forward/- and backward/+ orientation reads/breaks. Viral integration detection software has a similar history of implicit usage of loose ends/single breakends without explicitly using either terminology (only the recently published VIRUSBreakend uses the term).

In summary, this paper would benefit from briefing mentioning the long history of the loose end concept, and how it has been incorporated into existing tools.

Some additional thoughts to consider:

One interesting benchmarking comparison you could incorporate is against WEAVER. It also generates junction-balanced breakpoint graphs using integer programming, but its conceptual model does not appear to include single breakends. In my benchmarking (https://doi.org/10.1101/781013, Figure 3), I found that weaver failed badly on some samples and I suspect this was due to missing high copy SVs causing all junction balancing solutions to be terrible (thus reporting unbelievable ASCNs). Comparing to WEAVER (or comparing jabba MIP results with/without single breakend support) would be a good demonstration of how essential single breakend support is to the junction balancing process itself.

we found that almost half (48%, 12,068 of 25,271) of loose ends arose from Type 0 junctions that were missed during genome-wide analysis”

Is this a consequence of waiting till after SV and CN calling is done before looking for single breakends or due to the choice of caller? Would another SV caller (e.g. manta) reduce this? How many of the single breakends found by jabba can be found by stand-alone single breakend SV calling (e.g. GRIDSS2)? I notice jabba allows a BND style VCF input. Does it support single breakend BND calls?

Single breakend from SV calling and single breakends unbalanced CN junctions seems very much like they are complementary approaches so combining them should improve the final jabba results. I suspect this will be especially true for complex events as they frequently containing many clustered SVs and accurate copy number determination becomes more difficult the shorter the CN segments become.

On 2021-06-08 21:04:01, user Charles Warden wrote:

Also, I am waiting for my other comment to be approved, but I think the template for Figure 5C-G was used for Supplemental Figures S6-S13 (without shifting the letters to begin with "A," for each separate cell type)?

Thank you again for developing this tool!

On 2021-06-08 18:04:03, user Charles Warden wrote:

Hi,

Thank you very much for posting this preprint.

I am working on trying to read through the manuscript more carefully, which I hope can improve my understanding of STARsolo as well the regular STAR alignment. I also thought the different results with varying settings of Alevin was interesting and important.

However, in the meantime, I believe that you have a minor error in one of your references:

[30]. R. S. Brüning et al. Comparative Analysis of Common Alignment Tools for Single Cell RNA Sequencing. preprint. Bioinformatics, 2021. doi: 10.1101/2021.02.15.430948.

I think this should be a bioRxiv preprint (not a Bioinformatics preprint)?

For example, the DOI leads to this reference:

https://www.biorxiv.org/con...

Thanks Again,<br /> Charles

On 2021-06-08 19:43:21, user Seth Vigneron wrote:

Summary:<br /> This manuscript by Mikl, M., et al, aims to understand how RNA transcript subcellular localization signals are encoded in 3’ UTR sequences. To this end, the authors designed an MPRA to test thousands of 3’ UTR sequences in parallel. The authors transfect the library to neural cells grown in microporous membranes which allows them to separate the soma from the neurites and subsequently sequence the transcripts in each. The results from the MPRA demonstrate that only a subset of transcripts are enriched in the soma or neurites fractions and localization signals encoded in the 3’ UTR are sufficient to drive transcript localization. The authors then validate a subset of their enriched transcripts via smFISH demonstrating their MPRA mimics endogenous transcript localization. The authors proceed to analyze the sequence of enriched transcripts via mutagenesis and insertions which elucidates that RNA binding proteins (RBPs) largely prevent localization of transcripts to neurites. The authors then follow up their investigations with the creation and validation of longer, novel synthetic 3’UTR sequences capable of neurite enrichment, with subsequent biochemical pulldowns of cell lysates identifying RBP’s necessary for localization. Utilizing their vast dataset of 3’UTR localizing motifs, the authors generated two computational models, one trained on known RBP binding sites and the other assessing all possible sets of 4mers within the sequence, that could successfully predict the localization behavior of unseen 3’UTRs through the estimation of the combined contributions of multiple individual directing sequence elements.

The major success of this manuscript is in the development of a high-throughput assay to elucidate 3’ UTR encoded transcript localization signals and generation of machine learning models that predict subcellular transcript localization. Overall, we think this manuscript is of high impact and relevance to understand the mechanisms underlying mRNA transcript localization.

Below are the major and minor points that should be addressed before the manuscript is published to aid interpretation.

Major Points:<br /> A major concern we have is that the authors mention previous transcript localization studies have very little overlap on enriched dendritically localized transcripts. The authors attributed the lack of overlap to different experimental set ups and cell-types used. Therefore, the manuscript would be improved by adding a brief explanation as to how their experimental set up and cell types used contrast with previous methods and why their approach might be a better method to identify localization signals encoded in the RNA transcripts. Is there any agreement with previous studies that shed light on biases of the different approaches? Comments on these points will assure readers of the broader significance of their findings and not just the cell type used in the study.

Reasoning for the cell type used (CAD and Neuro2a cells) is not explained until the discussion and when mentioned it is not very clear. The manuscript would benefit from a brief explanation of cell type choice when authors explain the final library is transfected into CAD and Neuro2a cells in the results section.

Regarding the differentiation protocol of Neuro2a and CAD cells, the authors mention in the methods section that they induced differentiation via serum starvation to differentiate cells into a “more neuron-like phenotype”. However, they do not specify at what day post-differentiation the MPRA experiment is done. Consider adding the day of differentiation assays are done. Also, the manuscript would greatly benefit from IF, qPCR, or WB for neuronal markers to know the cell-type population used in this study, as transcriptional control is largely cell-type dependent.

Minor Points:<br /> Not clear if or how the author's account for the effects differential expression of transcripts and transfection of constructs might have on their output library.

Figure 1A: The experimental outline can be improved to aid the reader understand the library design. The construct used in the library could be edited to include what promoter is upstream of GFP, GFP, the 12 nucleotide barcode, the 150 nucleotide sequence, and the pA-site.

When the authors test the hypothesis that localization potential in RNA is broadly encoded in the 3’ UTR they refer to the experimental setup from Taliaferro et al., 2016 (second line on page 7). To make the experiments clearer for researchers across fields, we suggest adding a brief explanation of the experimental set up.

Figure 2: This figure could be improved by re-organizing the order of the panels such that it is easier for the redear to follow the panels from A to F.

Figure 2D: Not entirely clear why they include St6gal1 on figure 2D without mentioning in the text. We suggest adding a sentence explanation in the main text.

Figure 2D and 2E: For smFISH images and quantification, was there a control construct with just GFP? If data is available, the authors should show the image of the ‘normal’ distribution of GFP and then use it as a normalization control for their quantification on 2E.

Figure 2: No example graph of a broadly encoded transcript is included. Since this is a major conclusion from the paper we suggest the graph to be moved from the supplementary figures to figure 2.

In the main text when authors explain the broadly encoded signals might have “many small contributions making up the net localization behavior” it is not clear what they mean by that. A brief explanation of what “small contributions” could be will help make their results more clear to the reader.

For RNAi experiments, it is not clear the extent of knockdown for targets as qRT-PCR data mentioned in the methods section is not presented. The qRT-PCR data should be included in the supplementary figures.

When AGGUA is inserted 1 to 4 times (5th line on page 9) Where is the sequence inserted (at what position(s), throughout the transcript, one after another, etc.)?

After the knockdown experiments the authors state that “Dazap1 is one mechanism underlying soma enrichment”. To ascertain this is the mechanism responsible for retention of transcripts in the soma, the knockdown experiments could benefit by the addition of rescuing DAzap1 and see if that rescues the negative effect.

It is unclear as to how the MEME Suite generates the de novo synthetic sequences, how many were generated, and what was the range in sequence lengths. A brief, yet more explicit description in the main text of how these synthetic sequences were generated and then ‘introduced in native contexts’, e.g. were they added to the end/beginning/within existing 3’UTRs, would help the reader better understand your experimentation.

Figure 4B and 4C: The vast majority of the synthetic motifs appear to be shifted towards more negative logFC’s indicating increased soma localization. While the success of SU1 is impressive, the low replicability should be mentioned as a caveat in the main text and it’s potential causes speculated upon in the discussion.

The analysis of the proteomics data should be better explained either within the text or figure captions. Figures 5B, 5D, and 5E are very difficult to understand without any explanation as to how to interpret them in the text.

Figure 5: It appears that the plots in Figure 5D and 5E have been switched based on their references in the main text.

The font size of Figure 5C, 5D, and 5E is much too small to be legible and easily understood.

Figure 5F: It would greatly help with clarity for the meaning of the red vertical line to be indicated within the plot itself and not solely within the figure caption as it is vital for data interpretation.

Consider adding more background into why Celf1 and Celf6 were chosen for validation over the other 23 identified proteins. It would be valuable to state the known, or utilize experimentation to determine, the pathway by which these proteins binding to the 3’UTR shuttles them to the neurite. In other words, what is the entire mechanism for neurite localization, not just the identity of the RBP.

There is an inconsistency in the spelling of ‘4mer’ (as spelled in the main text and caption) and ‘fourmer’ as it appears in Figure 6A. There is also never a direct definition of what the 4mers are and what information they convey to the computational model.

Some speculation into the power of your computational model would be helpful in the determination of its use in future projects. How might further iterations and optimizations be done to improve the auROC?

Reviewed by Seth Vigneron (UCSF) and Dianne Laboy Cintron (UCSF)

On 2021-06-08 13:03:02, user Paul wrote:

IMPORTANT: We no longer stand by the results of this manuscript.

Since releasing this pre-print, it has been brought to our attention that using the Martini model of cholesterol with the default LINCS parameters for GROMACS leads to unphysical temperature gradients across bilayers (see Javanainen et al, https://arxiv.org/abs/2009..... We used the new-RF parameter set for running Martini simulations on GROMACS (de Jong et al., http://www.sciencedirect.co...:JjdGaZsuH-pi48Tk6hpCn0eUiRc "http://www.sciencedirect.com/science/article/pii/S0010465515003628)"), which uses the standard LINCS parameters (lincs_iter=1, lincs_order=4) rather than the more conversative parameters that the cholesterol model was parameterised with (lincs_iter=2, lincs_order=8). We have since performed our own investigation and confirmed that there is a temperature gradient of around 100 K between the ordered and disordered regions of the membranes simulated in this manuscript. Also, when we applied the more conservative LINCS settings we no longer observed phase separation. We therefore believe that the disruption of domain formation by cholesterol oxidation is no longer supported by the simulations and is instead an artefact of the aphysical temperature gradient that results from using the less conservative LINCS settings.

On 2021-06-08 12:15:43, user Serge wrote:

Very interesting data and more insights in the origin and heterogeneity of the different lymph nodes. However, Im afraid that the statement that endothelial cells initiate the embryonic LN formation is incorrect or at least one-sided (page 3, 2nd paragraph). Even without the presence of lymphatic endothelial cells (LEC, to which this study is referring), initiation of LN formation still occurs. We have shown clearly that in the absence of the LEC, Cxcl13 expression is present (NatImm 2009, PMID 19783990, figure 2e). Also, in Prox1 KO embryos, lacking all LECs, LN anlagen were still observed (Development 2009, PMID 19060331). LECs are very important for increase of the LTi cell cluster (but not for the initial clustering), as we and others have shown (e.g. in the beautiful study by the group of Petrova, JEM 2018, PMID 30355615). In short, retinoic acid, not lymphotoxin, is the first to induce Cxcl13 expression in the mesenchymal cells (NatImm 2009). The source of retinoic acid is not completely clear yet, but is most likely not to be endothelial (certainly not lymphatic). Also without lymphotoxin LN initiation also occurs, but further development is halted around E14.5 and the LTi cluster consequently dissipates.

I really hope the statement on initiation of LN formation can be improved before publication in a peer-reviewed journal.

On 2021-06-08 11:20:16, user Damien wrote:

Thank you for this nice paper ! I think "changes in N (28,880 GAT>CAT, D3L)" should read 28280

On 2021-06-08 02:23:10, user Daniel J Paluh wrote:

The peer-reviewed paper is now published at eLife: https://doi.org/10.7554/eLi...

On 2021-06-07 21:57:11, user Fraser Lab wrote:

Summary:<br /> Within this manuscript, authors describe the antigen specific T cell response to SARS-CoV-2 mRNA vaccines. Both vaccines induce robust antibody and memory B-cell responses after two doses, but the kinetics and nature of the antigen specific T cell response are less well-characterized. In this longitudinal study of SARS-CoV-2 naïve and recovered individuals, Painter et al. aimed to characterize the antigen-specific CD4+ and CD8+ T cells response by 1) comparing differences in the kinetics of the CD4 T cell induction in both cohorts, 2) characterizing the differentiation state of vaccine-activated T cells, and 3) performing an integrated analysis of 26 measures of antigen-specific immune response to better characterize the immunological underpinnings of mRNA vaccine-mediated immunity. Their findings elucidate a coordinated immune response in both SARS-CoV-2 naïve and recovered individuals following mRNA vaccination that mimics a response to natural infection. Additionally, these data highlight the importance of characterizing the antigen specific T cell response during the development of future booster shots.

Major Points:

• Although we are unfamiliar with the process of obtaining participants for SARS-CoV-2 vaccine studies, the study cohort seemed small and predominantly white. The SARS-CoV-2 naïve group had 29 participants and the recovered group had 10 participants. Of the 39 total participants, there was one Native-identifying candidate and two Black-identifying candidates based on Table S1. It would be helpful to address the study size and demographics to discuss whether you might expect these results to be representative of the US population.

• Along these same lines, the paper did not include details about the severity of illness in SARS-CoV-2 recovered participants or the amount of time since infection. It would be helpful to include these details as well as a sentence in the discussion about how these factors might be expected to influence the results.

• Based upon Table S1, it appears that SARS-CoV-2 naïve participants all received the Pfizer vaccine, while 30% of recovered individuals received the Moderna vaccine. It would be useful to add a brief commentary about how authors accounted for different vaccines in their analysis and if there were any observed differences based on the vaccine administered.

Minor Points:

• PBMCs are collected at four time points: pre-vaccine baseline (timepoint 1), two weeks post- primary vaccination (timepoint 2), the day of the booster vaccination (timepoint 3), and one-week post-boost (timepoint 4). A short explanation rationalizing why these time points were selected may be beneficial for those who are less familiar with the kinetics of T cell responses.

• We would have liked more explanation of the markers used in the characterization of AIMS (activation induced marker expression) in the introduction. It would be useful to explain what each of these markers detects and why it is correlated with the activation state, perhaps with a reference to a previous publication.

Submitted by James Fraser on behalf of the anonymous reviewer(s) as part of https://fraserlab.com/peer_...

On 2021-06-06 15:55:16, user Xingyu Liao wrote:

SRC is publicly available at https://github.com/BioinformaticsCSU/SRC

On 2021-06-06 05:13:39, user Stuart Newman wrote:

What is described here is a "morphodynamic" mechanism, as defined in this paper https://pubmed.ncbi.nlm.nih...

On 2021-06-05 10:20:07, user Marc Robinson-Rechavi wrote:

Under Data and code availability, the authors write:

The code for evolutionary simulations together with sample notoebooks and data used in the article will be made available on GitHub along with the publication of the manuscript.

This is a publication, i.e. it is made public as part of the scientific record and is citable, thus I strongly invite the authors to make the corresponding GitHub available without delay.

On 2021-06-04 18:54:07, user jasonrasgon wrote:

We are aware of an error in this manuscript regarding the small RNA analysis, the data have been reanalyzed and a corrected version will be uploaded shortly.

On 2021-06-04 16:07:21, user Andrew Alamban wrote:

“A biosensor to gauge protein homeostasis resilience differences in the nucleus compared to cytosol of mammalian cells”. Raeburn et al.<br /> doi: https://doi.org/10.1101/202...<br /> Reviewed by Andrew Alamban* and Linh Tram*<br /> *University of California San Francisco

Summary:<br /> In the cell, there is an extensive network of protein quality control machinery that maintains protein homeostasis. A disruption in this network may lead to protein aggregation, which is a hallmark for many neurodegenerative diseases. This has prompted a need to develop a biosensor that can measure chaperone activity in the cell, which the authors have done in their previous work (Wood, R. et al. 2018. Nat. Comm.). One way to gauge chaperone activity is to measure their ability to bind unfolded proteins, also known as “holdase” activity, to prevent aggregation. We found that the authors give a helpful explanation of how their previously-designed biosensor works, reducing the need for the reader to reference the previous publication.

In this manuscript, the authors improve upon this tool to include nuclear localization or export sequences (NLS or NES, respectively) to probe protein homeostasis in the nucleus or cytosol, respectively. This control of biosensor localization is very impressive. Using this new capability, they show that 1) holdase activity in the cytosol is more abundant than in the nucleus and 2) imbalance in protein homeostasis - by co-expressing the huntingtin exon 1 mutant - can reallocate chaperone supply in different areas of the cell.

A long-standing view in the proteostasis field is that the quality control machinery is more abundant in the cytosol. Their new biosensor supports this view by showing that there is more holdase activity detected in the cytosol than in the nucleus.

The authors show that Huntingtin (Htt) inclusions can affect the fluorescence analysis of cells via flow cytometry. We appreciate that they addressed this limitation of their biosensor. They propose a workaround by measuring FRET using microscopy instead of their flow cytometry method. Using this workaround, the authors find evidence that the cell can reallocate quality control machinery between the cytosol and the nucleus.

By adding the NLS or NES, the authors have extended the biosensor’s capability to answer more questions about proteostasis. While the constructed biosensor only used barnase, which binds to Hsp70 and Hsp40 family chaperones, as the model protein, the scheme suggests a potential to expand the scope of the biosensor by using different model proteins that bind other quality control proteins beyond Hsp70 and Hsp40 families.

Major Points:

The authors modify their previously-developed biosensor to restrict its localization to either the cytosol or nucleus using an NES or NLS, respectively. Because protein folding is essential to the biosensor’s function, the authors validate these new modifications by measuring protein stability via urea denaturation of the wild type* (WT*) barnase. The authors only perform the validation for the WT* but not for the mutants. Could the differences in the lower slope gradient observed in Figure 2B for the mutants be due to the NES or NLS affecting the mutant barnase stability differently than WT*?

There seems to be a discrepancy between data from Fig 2B and Fig 3B. Fig 2B shows that there is a lower slope gradient in the cytosol than in the nucleus. Looking more closely at Fig 3B, it almost looks like the nucleus has a lower slope gradient than the cytosol. This contradicts the conclusion from Fig 2B that the cytosol has more holdase activity when in Fig 3B, it looks like the nucleus has more. How could these differences be reconciled?

Minor Points:

Introduction:<br /> In page 1 line 57, the abundance of unfolded-like barnase is not detected by FRET but rather by the absence of FRET

Duplicate citations on refs. 5 and 6

In the paragraph that starts on page 1/line 59, I was able to understand the motivation for creating the biosensor. However, the authors go on to explain that they added localization sequences without motivating a reason for why the comparison between the nucleus and the cytosol is important. The authors have this information in their discussion (line 226-227) and a brief mention of this in the introduction would help motivate the study.

Methods:<br /> In line 270, it was unclear to me what it means to “decouple the expression of the two plasmids”. More detail in this section would also help in the ease of reproducibility of the work.

Catalog numbers should be included for all materials

In line 280, there’s a typo. “Ovine” should be “bovine”

We like that the authors provide scripts alongside the example datasets for their image analysis. This aids in reproducibility

Figure 1:<br /> Labeling style for Fig 1A could benefit from the cartoon in the style of the (Wood, R. et al. 2018. Nat. Comm. Fig. 1), where the conformations of the bait, as well as the other proteins, were explicitly shown

We are curious about how the linker control was designed since the linker control was not introduced in the initial biosensor paper (Wood, R. et al. 2018. Nat. Comm.) Which factors determine the linker control’s length and its amino acid sequence?

It looks like both localization sequences (NLS and NES) are appended to the biosensor in Fig 1A, which contrasts with what described in the Results.

Fig 1D, unclear that they didn’t label “D” and “A”

Mentioning that urea acts as a denaturing agent would be helpful, especially to newcomers unfamiliar with the assay

Figure 2:<br /> Figure 2C: How was the percentage of cells with aggregates calculated? Legend of the figure suggest that the percentage is derived from the ratio (upper slope)/(lower slope)

In Line 113-114, the authors observed that the I25A I96G mutant was potentially outside of the detected dynamic range of the biosensor. However, the I25A,I96G mutant was still used in subsequent experiments without providing further explanations.

Figure 3:<br /> Fig 1 and 3, using the same color for the Hoechst dye would help better with continuity across figures

What drove the choice for using the Y66L Emerald as the transfection control rather than an empty vector?

Figure 4:<br /> It would be useful to see a color map for the FRET map on the side to get a better idea of the range

What does white or red arrow mean in figure 4? We think that the white arrow indicates inclusion-targeted and the red arrow indicates diffuse-targeted

The signal that the white arrow is referring to in Figure 4A for the nucleus is barely visible

In Figure 4, would it be possible to use different line styles for the WT* and the mutants?

In Figure 4, WT should be labeled as WT*

On 2021-06-04 11:22:19, user Mick Watson wrote:

Have you tried this with metagenomics?

On 2021-06-03 14:43:20, user Arsen Arakelyan wrote:

Thanks for the paper, I was wondering if you have an experience with flongle for cDNA sequencing? What is the average output?

On 2021-06-03 13:52:31, user Chris wrote:

Abbreviating AUROC as AUC is awkward - AUPR is also an AUC metric (that has different characteristics to AUROC).

On 2021-06-03 05:36:41, user Dr. Anup Som wrote:

This preprint has been published in Indian Journal of Biochemistry and Biophysics. <br /> Paper Link:<br /> http://op.niscair.res.in/in...

On 2021-06-02 19:55:27, user Charles Warden wrote:

Hi,

Thank you for posting this preprint.

As a minor point, I think there is some grant information missing:

"National Institutes of Health grant X (CBB)"

Best Wishes,<br /> Charles

On 2021-06-02 14:17:58, user Rob Patro wrote:

This is an interesting approach, and the results look quite promising. In particular, the semi-reference-based compression scheme adopted in RENANO_2 that frees the decoder from having to have access to the exact reference used to compress should make the tool easier to use in a broader variety of cases. I just want to point out what may be a relevant citation for the semi-reference-based compression idea in a technique my student and I developed a few years ago (focused on short-read compression) : https://academic.oup.com/bi.... Congrats on the great work!

On 2021-06-02 06:26:47, user Claudio Tennie wrote:

The following is PART 3 (of 3) of our response to Mielke (we had to split up our reply, due to character limitations here on disqus)

The claim that “the simulation rules used are undistinguishable from copying”.

Answer: This is an opinion that was also voiced by another participant in the original twitter debate and so we shall explain in more detail. In that twitter debate we already mentioned that they can be clearly distinguished, but that the difference underlying them is often not acknowledged or implemented. The resulting confusion is based on the tendency in other cultural modelling work (indeed, in most cultural modelling work) to blackbox and exclude the details of form copying. In our model, as all behaviours are latently present in the individuals (i.e. can individually be reinnovated) there is no need to copy new behaviours (and with it, no need to introduce new behaviours). This is because the simulation rules never implement the necessary copying. This exclusion of form copying is by design - in our model. The fact that the output of this our model of non-form-copying is indistinguishable from real life ape culture - or other cultures identified by the method of exclusion - is exactly the point that we are making.

Form copying is best defined as the causal copying of the actual details of demonstrated forms - i.e. their internal and/or linear structure to each other (Tennie et al. 2020 Bio & Phil). In other words, the know-how, must be causally transmitted. It is easy to see that the way in which most cultural models are implemented do not in fact model form copying in this way at all. In such a model, typically an agent might, for example, be faced with the problem of “copying” the production of a kayak. But the way that this is modelled then is usually by assigning a certain likelihood that a kayak is later produced by the observer. But then, none of the actual details of the kayaks are causally copied here - the kayak is either developed by this agent after observation, or it is not. But here is the catch. The kayak design cannot evolve using this type of model. But in real life the kayak design is even bound to (!) evolve culturally - via copying error alone (as this type of error is unavoidable). These models are often modelling a type of match that can in principle be solved either by copying or by socially mediated reinnovation - that is, by mere triggering. Another way of making clear the lack of actual form copying in these models is this: such models could not recreate the outcome even of the “telephone game” as played by children. This is because the initially whispered message (e.g. “the fox jumps over the fence”) cannot culturally evolve alongside the whispering chains in such models. The “funniest” outcome here would merely be the failure to pass on this message (after which there would be no more message at all transmitted further down the line). Therefore, the critique raised here by Mielke and others and in the original online twitter debate is not relevant. It is not, and cannot be, our responsibility that the field does not usually model real life form copying.

It would seem that the lack of form copying is a potential shortcoming of this field of modelling. When the explanatory target involves actual form copying in one way or another then such a model will no longer work, will no longer be useful (however, note that the explanatory target of many of these models are nevertheless unaffected by these particulars). Thus, for example, any good model of the telephone game must truly implement form copying (the details of the sentence must be attempted to be copied).

In our model, instead, we intentionally chose this very model design - i.e. one that is lacking form copying - and we choose it precisely because (!) it excludes form copying. We fully required the implementation of a mechanism that absolutely cannot copy form to test if form copying is and must be necessary before wild ape cultural patterns can be reproduced (or, more generally, before general positive outcomes of the method of exclusion can be reproduced). Ours is therefore a null-model. Contra Mielke’s claims, our socially mediated reinnovation is therefore not form copying - it can be clearly distinguished from form copying, by not transmitting the necessary details. Our model would not be able to produce real life outcomes of children's telephone games even. But again, this is intentional - it is so by design in our model. Our guided reinnovation of form A after social contact with form A is socially mediated reinnovation - it is a social triggering of this form in another. We know from experience that this implementation is unintuitive to us humans, precisely because humans base nearly everything they do instead on form copying. Were this not the case, and were human behavioural forms more often merely triggered, we would have a much easier time publishing our papers. Unfortunately for us, humans rarely show such triggering, and when we do, we do so in ways that do not closely match the types of learning underlying ape cultures (who are triggered in this way; see above). Nevertheless, it is still at least illustrative to consider such a case: a yawn merely triggering a yawn in another human does not transmit the yawn’s form (even blind-born people yawn). Again, this is being proof of principle, that not all culture needs form copying. Details in the ape case differ to yawning - but the outcome (triggering, not copying) is the same.

Needless to say, this difference (form copying yes or no) matters especially in the long run. With mere socially mediated reinnovation, a system is essentially restricted to the kinds of forms that it can self-produce (i.e. it is restricted to its zone of latent solutions; Tennie et al. 2009). Instead, humans are not restricted in this way, due to our reliance on actual form-copying. Here, error-copying alone will ensure, over time, and in a path-dependent way (!) that more and more forms are not only being produced, but also copied and maintained. This has two very strong consequences (e.g., Tennie et. al. 2020 Bio & Phil; Motes-Rodrigo & Tennie 2021). 1. This will produce forms that no individual could reinnovate anymore (as Richerson & Boyd have originally pointed out; or what we call copying-dependent forms; Reindl et al., 2018) 2. This will create a large number of these types of forms. Indeed, both effects can clearly be seen in humans - humans show billions (!) of copying-dependent forms by now (Motes-Rodrigo & Tennie 2021). This contrasts with the few thousands shown by the other apes combined, of which only zero to three show noteworthy indirect evidence for being copying-dependent (Motes-Rodrigo & Tennie 2021). Overall, ape behaviour is currently best explained instead via the ZLS account - in at least most cases, if not all - and our oranzee model is another piece of the puzzle that shows this to be the best explanation.

In summary - across all three parts of our response - we thank Mielke for correcting our ‘specifics claim’ (see Part 1 of our response), which we have therefore removed from our manuscript - but we disagree on the other claims Mielke raised, for all the reasons given in our remaining response (Parts 2 and 3).

Claudio Tennie and Alberto Acerbi

We thank Elisa Bandini for helpful comments on an earlier draft of our response.

On 2021-06-01 17:42:44, user Claudio Tennie wrote:

We have uploaded our response to the main point rasied in Mielke’s 2020 bioRxiv comment on our oranzee MS elsewhere (below his original comment). Due to character limitations of disqus (or in any case upload issues we experienced) we will now answer the remaining points here. Having answered Mielke’s main point, below, we will therefore only answer to Mielke’s additional points where he a) directly claims to critique us beyond a critique of our specifics claims and/or b) where we deemed that Mielke raises points that might appear to readers to apply beyond a critique of our specifics claims. Given that we can show with data how and why these critiques are not relevant (see below), and given that the appropriate literature containing this data is and was already cited in the manuscript, we have not changed our manuscript based on these comments addressed below (although note that we have since worked on the manuscript more generally, and therefore it is likely that these points are now made clearer in the new manuscript). Note that we experienced upload issues again here at disqus when uploading our reply, which is why we spplit our reply. This here is PART 2 of our reply. A third part will follow.

The claim that we deny the ecological importance of ape culture. E.g. Mielke writes “The model, and I would say the theory underlying it, ignore that an ape who fails to learn a skill correctly faces immense costs.”

Answer: We do not ignore the ecological relevance of ape cultures, and never did. As for the implication by Mielke - that copying is necessary for ape cultures - this is a widespread idea, but it is empirically unsupported. Apes do not require copying to acquire even their most complex behaviours (e.g. even nutcracking with hammers can be reinnovated from scratch (shown by Bandini et al. (accepted with minor revisions); available at https://www.biorxiv.org/con.... Therefore, while it is true that apes have to learn, the question we keep on asking is: how do they learn it? We already laid out how they do so (based on the relevant literature) in our original manuscript. In sum, and as reflected already in our original manuscript, the evidence points away from form copying, and supports socially mediated reinnovation of know-how. See more on this below.

The claim that a lack of certain social learning biases in our model renders our model invalid. E.g. Mielke writes “So, if learning probability in the simulations is based on the frequency a behaviour is observed in the population, treating all potential models evenly and not weighting the impact of potential models by their age (e.g. remove infants and juveniles) biases the outcome of the results.”

Answer: Our general results do not depend on such specifics of social learning biases. Specific outcomes (e.g. exact number of cultural traits) do, but we no longer make claims based on such specifics (i.e. we no longer make the ‘specifics claim’, see above). In fact, social learning biases could be easily added to the model, but note that, because of the stochastic nature of some of them (e.g. prestige bias) their addition may even be likely to increase the probability of finding distributional “cultures” without form copying.

The claim that there is an “open-endedness” to ape culture in real-life and which needs to be inbuilt into our model. E.g. Mielke writes “There are hundreds of different ways to groom someone.”.

Answer: In theory, there could be hundreds of ways to groom - thousands even. It is therefore all the more surprising - but only under the assumption that apes regularly copy forms - that, in this case and across cases, apes are nevertheless empirically restricted towards certain forms, and which are few in number. Indeed, in a first, indirect “ballpark-count” it was recently concluded that apes are thus biased towards only a few thousand behavioural forms overall, across all ape species, behavioural domains (incl. grooming) and populations (the wild included; Motes-Rodrigo & Tennie 2021 Bio Rev). This is in heavy contrast to the human case, who have many more behavioural forms; indeed counting not in thousands or even in millions, but in the billions (Motes-Rodrigo & Tennie 2021). Therefore, whilst the theoretical logic proposed by Mielke holds - it only holds for humans in real life, but it does not hold for apes. Across our publications, and all considered, we continue to explain the most parsimonious reason why this is - ultimately, this difference derives from apes not basing their behavioural forms on copying. Instead, they seem to instead trigger forms that they latently possess (latent solutions).

Having a finite number is a simplification for modelling purposes. In our model we consider a finite number - 64 - of forms, but notice the specific number is arbitrary and does not change our main result. And, again, ape culture does not show signs of open-endedness in real life, so, strictly in keeping with Mielke’s call to make models more real-life like, we also do not see the need to implement open-endedness.

The claim that the meaning of social behaviours is equal to their behavioural form. E.g., Mielke writes “Play elements that nobody else knows will not lead to successful play.”

Answer: The question of how apes glean meaning from behaviour is a question that we did not study. We also fail to see the relevance of this comment to the source of behavioural form. Meanings might be related to ‘this or that’ factor, yes. However, none of this determines the behavioural form itself, and which is what our manuscript discusses.

The claim that the available data regarding ape social learning must be interpreted as spontaneous form copying. E.g., Mielke writes “Apes have probably in access of 100 different play elements in each group (Nishida et al 2010; Petru et al 2009), and it can easily be expected that innovation and social transmission occurs in this context (Perry 2011).”

Answer: Apes fail to copy forms under controlled settings (unless this skill is artificially planted via training and/or enculturation), and ape’s behavioural forms are reinnovated across populations and to a large extent, even across ape species (Motes-Rodrigo & Tennie 2021 Bio Rev and references therein). This should be expected, given that apes reinnovate these forms from scratch (and this is including social behavioural forms; e.g. handclasp grooming, mentioned by Mielke, is a nice point in case as its (few) various subforms also emerged across culturally unconnected populations, including in captivity). It is likewise irrelevant for questions of form copying whether a behaviour involves multiple individuals (Mielke: “rain dancing, cannot conceivably be reinnovated by one individual – what would that even look like, given that it is a coordinated action of several individuals with no discernible physical function?”). To show this, let us take the example of bird flight: to form a V formation in the sky cannot be done by a single bird either, but in contrast to Mielke’s claim this specific fact does not answer the question of what leads to this V shape - what leads to this V form. The answer is, perhaps in this case, a large influence of the environment, i.e. aerodynamics in conjunction with socially flying birds. The exact drivers most likely will differ across cases (e.g., sometimes the genetic level may play more of a role than the environment), but the general point does not depend on these details. The main point remains that none of these factors can pinpoint form copying. The fact that the various raindance forms occur elsewhere however speaks against form copying (as we explain here: Tennie & van Schaik 2020, Phil Trans B - compare Motes-Rodrigo & Tennie 2021 Bio Rev)

The claim that our model cannot - but should - capture multi-step behavioural forms. E.g. Mielke writes “Many of the described behaviours in Whiten et al 1999 are not simple behaviours that occur in a vacuum, but action sequences with several elements that have to be fulfilled in the exact right order and are embedded in sequential behaviour patterns; for example leaf clipping.”

Answer: We do not deny that ape behaviour can be complex and composed of multiple steps. Nobody we are aware of denies this. However, this, too, does not pinpoint form copying. To see why, consider this. A spider making a web is (and must be) using multiple steps in the correct order, too. But this does not mean that the spider must have copied this behavioural form [important note: we use the spider example as an illustration of the logical principle, we are not saying that apes learn just like spiders]. Another way of saying it is this: does multi-step behaviour require copying? It does not logically (see the spider example), but is there maybe a reason to assume that multi-step behaviour requires copying in the case of apes? If so, then we would agree. However, instead we know that multi-step behaviours do not require form copying in apes (e.g., see the empirical finding of ape nut-cracking reinnovation from scratch, using hammer sequences; Bandini et al (accepted with minor revisions)). We therefore must reject this notion on both logical and empirical grounds - despite it being intuitive and widespread.

As for the open-ended comment/aspect, If Mielke here refers to the fact that our model does not consider multi-step behavioural forms, again, this is a simplification for modelling purposes (and see also our notes on open-endedness above).

Claims regarding ‘known unknowns’. E.g. Mielke writes “detailed analysis will likely find that there are different ways of dragging a branch, as has been found for other behaviour on the list (e.g. digging for honey Estienne et al 2017).”

Answer: We would not like to engage with claims regarding known unknowns. Yet, note that some previous unknowns have been studied and thus turned into interesting knowns. For example, we recently ran a study on target-naive, unenculturated chimpanzees in which these nevertheless spontaneously developed a whole range of digging behaviours using organic tools - i.e. without the need for form copying. Again, we are not denying that apes show several behaviours - they clearly do (see above) - we are questioning whether any of these require form copying. Our study was designed 8among other things) to test the widespread claim that wild ape cultural patterns per se involve such copying and/or that they must involve such copying. Our study showed that, conversely, they do not. These aspects of ape behaviour do not pinpoint form copying. Another recently published study used a new, dedicated method for its search for ape form copying (the method of local restriction). It likewise demonstrated that most ape behavioural forms essentially auto-repeat. It also showed that the number of ape behaviours that show substantial (indirect) signs of being influenced by form copying in apes is extremely low. It ranges between zero and three (!) cases - across all ape populations, species and behavioural domains (Motes-Rodrigo & Tennie 2021 Bio Rev).

The claim that it matters how well our model states match real ape states. E.g. Mielke writes “Function and context might be specific to one sex or age-group: drumming in juveniles, for example, is often part of play; female chimps will slap the ground in displays rather than drum, even though drumming is sometimes observed.”

Answer: Our general results - and our main message - proved very robust and do not depend on these types of details.

The claim that our simulation was unbound by reality. e.g. Mielke writes “In general, it would be fantastic if there was even a basic description of why any of the simulations was designed as described here”

Answer: These descriptions were already part of the original manuscript, and several colleagues who had read our manuscript understood our approach. However, again, our newest manuscript is generally improved and clarified, so we believe that our new manuscript should be fully understandable (in addition to being replicable, as we lay open its code).

The claim that “‘Innovation probability’ is meaningless for social behaviours”.

Answer: Social behaviours are innovated just like material behaviours are, and so we fail to see a problem here. Indeed, one social behaviour in chimpanzees, handclasp grooming, has clearly been reinnovated multiple times across multiple culturally unconnected populations - including in captivity. More to the point of our manuscript, the source of the forms of these behaviours (in apes, at least) is very unlikely form copying (e.g. Tennie et al. 2020 Bio & Phil). In social and other contexts, apes can be triggered in various ways to reinnovate similar forms as those shown by their social partners.

The claim that the ape form copying assumption is still superior to the assumption of socially mediated reinnovation. E.g. Mielke writes “These seem to completely ignore anything we know about social learning or the life history of animals.”

Answer: We must strongly disagree, and indeed we do so on strictly empirical grounds. There is a long-held assumption of form copying underlying ape cultures, yes - but it has fared very poorly empirically. For some time, it indeed had appeared as if apes are spontaneously copying forms. However, claims for such spontaneous ape copying either had tested enculturated/trained apes (irrelevant for the question at hand as the skill is no longer spontaneous) or had merely tasked apes to seemingly (!) copy behaviours but that they could already do on their own. The problem here is that, clearly, things one can do on one’s own, do not need to be copied. Hence, any “copying” in these situations might have been an illusion of form copying. These results were then indeed proven illusionary in other, controlled studies - in studies that tasked apes with the copying of forms that they would not (!) already develop on their own (note, when human children learn behavioural forms, e.g. the word “laptop”, they are indeed learning forms that they would not otherwise produce). When tested in this way, unenculturated, untrained apes invariably fail to copy such novel forms - of either behavioural type (Clay & Tennie 2017 and references therein) or of artefact/tool type (Tennie et al. 2009 Phil Trans B). Note that we have another manuscript at the ready in which we additionally show that the failure of apes to copy in such situations is also not due to any social learning bias (and even ape mothers are not copied in such situations). Indeed, in stark contrast to human form learning (e.g. of the word “laptop”), ape behavioural forms repeat across populations and even species - and the overall number of ape behavioural forms is very small when compared with (form-copying) humans (Motes-Rodrigo & Tennie 2021 Bio Rev). The perhaps last possible objection that might be raised here, namely that maybe all these forms are still copied in the wild, but go back to some original cultural source population, can also be rejected. Not only would unavoidable copying error have led to a different picture today (Tennie et al. 2016, 2017), but when we test apes whose previous experiences are known and for whom any such cultural connected are effectively severed, they spontaneously reinnovate these forms, too ( including multi-step, complex behavioural forms such as nut-cracking with hammers; Bandini et al. (accepted with minor revisions)). Thus, truly taking into account everything we know about social learning of apes, the only available mechanism that can explain all these findings is that these forms are instead socially mediated, but not copied. Their form requires individual reinnovation (Bandini & Tennie, 2017; 2018). As a side note, Mielke also writes “by the time any chimp starts nut cracking, they will have observed several millions of strikes by their mother and other group members – are we to believe that they did not in any way take this information into account when acting?” Here, there can only be two answers in the light of the available data. First, socially mediated reinnovation happens in such cases, and therefore juveniles do absorb information (e.g. know-what (nuts), know-where (these trees) etc.; see Bandini et al. 2020, Biol Lett; Tennie et al. 2020 (Bio & Phil), Motes-Rodrigo & Tennie (2021)). Second, the idea that form copying is responsible for the similarities in behavioural forms between mother and offspring is strong and widespread, but it is - everything considered - most likely an illusion. relevant here is, again, that when tested at a later age, in the absence of demonstrations (note that orangutans do not crack nuts in the wild even), older, and therefore more individually (bodily) capable orangutans reinnovate the nutcracking form from scratch (Bandini et al) - and they can do so fast (for more and in-depth details on this comparison, please consult Bandini et al. (accepted w. minor corrections)).

The claim that an absence of evidence for form copying does not mean evidence of absence for form copying. E.g. Mielke then continues:“That reinnovation [of nut-cracking] is potentially possible does not rule out that most individuals in a community do not, in fact, reinnovate”

Answer: We have been very explicit in our manuscript from the start that our model does not allow for this claim. Instead, we did and do point to additional findings - for example, that apes do not copy novel forms, and that they spontaneously reinnovate the ones shown elsewhere (see also above). And so, the possibility of ape form copying playing any large role is rendered unparsimonious by that other, relevant, data. We merely apply Occam's razor across the available, relevant data. However, our model adds to this evidence as well. It helps triangulate the question by disproving one claim about what the method of exclusion can pinpoint.

The claim that innovation has no long-lasting effects in our model. E.g. Mielke writes “They don’t ‘reinnovate’ nut-cracking every time they are hungry, this renders the idea of innovation meaningless.”

Answer: This is simply a misunderstanding, as it is not how innovation is implemented in our model. Sensibly, innovation does lead to long-term consequences in our model. In particular, it does so by changing the “state” of our agents, i.e. when the agents innovate in a particular domain they (probabilistically) do not innovate any more within that domain.

The claim that our results do not provide relevant information. E.g. Mielke writes “However, the same thing is also true the other way round” in response to our claim that individual level mechanisms cannot be identified through population level outcomes.

Answer: This might have been true if our results existed in a vacuum. Yet there are many other, relevant types of data (cited above, and also in our manuscript), which in turn allow us to determine with high likelihood (using parsimony as our guide) the types of social learning mechanisms used by apes. The most parsimonious interpretation is that apes produce and maintain their cultures not via form copying, but via individual reinnovation of these forms which however is very often socially mediated (the latter bit renders these very clearly cultural, yes, but just not cumulative cultural in their forms).

On 2021-06-02 04:23:36, user VINODKUMAR SARANATHAN wrote:

v2 Now Published in PNAS:<br /> https://www.pnas.org/conten...

On 2021-06-02 02:15:13, user Jin Yu wrote:

Published PNAS online: https://doi.org/10.1073/pna...

On 2021-06-01 21:20:00, user Daniel Osorio wrote:

Dear Samuel,

Thank you very much for your interest in our work, as well as for your thorough review and comments. We will try our best to solve your questions below:

1. We agree with your point of view about the effect of a gene knockout on cellular homeostasis. In fact, in metabolic models where this kind of analysis is usually done using optimization approaches, the propagation effect of the gene knockout across several parts of the metabolism is evident. Nevertheless, Santolini and Barabasi (DOI: 10.1073/pnas.1720589115) compared the performance of the topology to predict the perturbation patterns caused by a gene knockout against the result of the optimization methods. They found a good overlap in the prediction, and based on those findings; we decided to use the topological approach. We did not try multi-knockout experiments since, as you mention single-cell RNA-seq characterization for those experiments is not yet available. However, we did try a double knockout and found a good overlap with the findings reported by the paper describing the dataset (Figure 3, Panel C). We yet do not have any other evidence to support or reject your hypothesis about the decrease of the precision of the predictions with an increasing number of knocked-out genes at the same time.

2. Since the regulatory link between two genes is assessed using principal components regression (PCR), the result after evaluating all the associations is a fully connected asymmetric weighted network. You may consider PCR as a partial correlation analysis (pcorr). When C1 and C2 are the same, pcorr(A,B|C1) equals pcorr(B,A|C2). However, in PCR, C1 is not equal to C2—C1 is all genes excluding B, while C2 is all genes excluding A. This asymmetry makes the result of PCR an asymmetric matrix. To further set the directionality of the resultant matrix, first, we removed the weaker link between two genes, and then, we filtered the links below the 95th percentile to reduce the false-positive rate. We provided evidence supporting that the true directionality of the regulation is favored by the regression method with a larger weight value (Figure S1, Panel C) when the directionality is tested using the transcription factors and their target genes reported by the ENCODE database. We also provided evidence of the accuracy of principal components regression to detect the association between genes in single-cell RNA-seq without imputation compared with other methods during the benchmark of scTenifoldNet (Figure 2, Panel A in DOI:10.1016/j.patter.2020.100139).

3. We are afraid we have to disagree with you on this. We did our best to perform an unbiased comparison of the gene knockout phenotypic effect reported by the authors of the datasets and the results provided by scTenifoldKnk. In fact, the characterizations made for the authors are not only based on data-driven approaches using the generated single-cell RNA-seq datasets but also include other experimental techniques. We used several gene-set databases to evaluate the extent of the overlap that we can predict, as it is recognized that a single gene or pathway often cannot fully explain a particular cellular state. Instead, biological processes are better characterized by gene regulatory networks, whose structures are altered as the phenotype changes (DOI: 10.1038/s41540-018-0052-5). We thought about reporting the result of scTenifoldNet and compare them with the results predicted by scTenifoldKnk. Still, since we are the developers of both methods, we decided to better compare our findings with the results reported by the original authors of the datasets. Please note that the original authors did not report all the changes or perturbed gene sets found after the gene knockout. We believe your experimental design is correct and feasible. However, also have in mind that not all the regulatory changes induced by a gene are detectable as changes in the expression level since a given gene may be under the regulation of more of one gene at the same time.

4. To evaluate the stability and robustness of the results provided by scTenifoldKnk, we used two approaches. First, we compared the results obtained by running independently scTenifoldKnk over two biological replicates in the Mecp2 example (Figure S2, Panel D) and found that the overlapping results agree with what is known about the Rett Syndrome pathology that is caused by the malfunctioning of the Mecp2 gene. Second, we resampled the cells used as input for scTenifoldKnk 10 times and compared the rank of the perturbed genes in the predicted in-silico knockout for each one of them. Since single-cell RNA-seq allows to uncover hidden subpopulations of cells with specialized phenotypes, and for that reason, by random subsampling the cells, we expect each of the constructed gene regulatory networks to be unique and provide a unique result. Because the approach is the same and the expected biological effect is the same (randomly sampling cells), we only performed the analysis over the Trem2 dataset. We expect the results to be similar in the other datasets.

Please let us know if you have any other questions or concerns,

Best wishes,

Daniel and James

On 2021-05-26 13:48:51, user Samuel Schäfer wrote:

Dear authors,

Thank you for sharing this interesting paper. I have myself speculated on how in silico knockout best can be implemented in a meaningful way and your paper therefore has sparked my interest further.

After reading your paper, I find that there is much to like about it. I appreciate scTenifoldKnk’s pioneering and minimalistic approach and share your view on the potential impact that in silico knockout predictions could have on experimental design of future studies. Reading your study with great interest I have some questions that I would like to forward to you in this forum.

1. As very briefly mentioned in the manuscript, synergistic effects of knockouts can be hard to explore experimentally as the number of possible knockout combinations can be large. Undoubtedly, a tool like scTenifoldKnk could prove incredibly valuable in guiding future experimental designs. From my understanding of the current scTenifoldKnk design the GNR approach assumes that the GNR in a knockout individual corresponds to the GRN in a healthy individual after removing all edges to the knockout gene. It is however quite imaginable that the introduction of a knockout to an organism not only leads to a disruption of edges from and to this knockout gene but rather to a distortion of the global equilibrium of the network. Introduction of a knockout to an organism could, at least hypothetically, lead to network adaptation in the form of edge weight changes or introduction of new edges. As you, from my understanding, are not considering that the steady-state confirmation (edges, edge weights, etc) of the wild type GNR could change upon introduction of one knockout, arguably your predictions precision should decrease with an increasing number of knockout genes. Have you tested this somehow? Would it be possible for you to validate how well scTenifoldKnk performs for multi-knockouts (by including more than one multi-knockout data set)? If such data sets can’t be found for mice / human perhaps they could be found for other organisms such as flies or bacteria.

2. When you develop the single cell gene regulatory network (scGRN) you describe that you derive directions from the principal component regression. How exactly do you derive edge direction from a regression analysis? I could not find this specifically described in the results or methods; would you mind explaining how this is done in more detail?

3. Though you briefly state that your analysis of the Nkx2-1, Trem2 as well as the Hnf4a + Hnf4g data set recapitulates findings made in the original studies, it became apparent to me that you do not present a systematic comparison between your findings and the original studies’ findings. Similarly, this is true for the Mendelian diseases, where you claim that findings are consistent with the known pathophysiological changes of these diseases, without having specified which genes are known to be involved in the diseases and in what way / to what extent findings are consistent. This, I find, makes it difficult to understand how much of the original articles results / known pathophysiology is recapitulated by scTenifoldKnk exactly and therefore makes evaluation of the usefulness of your approach difficult. While Table 1 certainly is of help, I think description of the original studies is still lacking depth. Therefore I was wondering if it would be feasible with a more systematic comparison between the virtual KO-perturbed genes / enriched gene sets identified by you and the genes / gene sets identified in the respective original article? Perhaps Jaccard similarity scores or similar scores could be calculated to quantify the similarity between your and the other studies’ findings?

4. Why is Spearman average rank correlation coefficient presented only for the robustness of the Trem2 data set and not the NKx2-1 and the Hnf4a + Hnf4g data set as well?

I very much look forward to seeing your work published in a peer reviewed journal and hope you find the time to answer my questions!

Best regards,<br /> Samuel Schäfer<br /> MD, PhD student<br /> Linköping University, Sweden

On 2021-06-01 19:17:24, user Eleonora Leucci wrote:

Coordination between the two translational machineries and its role in proteostasis was already shown in mouse and human cells and their desynchronisation for therapeutic purposes proposed. Here a few readings in case you want to acknowledge the authors...<br /> -https://www.cell.com/cell-r...<br /> -Nature. 2016 Mar 24;531(7595):518-22. doi: 10.1038/nature17161.<br /> -Nat Struct Mol Biol. 2018 Nov;25(11):1035-1046. doi: 10.1038/s41594-018-0143-4. Epub 2018 Oct 29.<br /> -bioRxiv 2020.06.26.173492; doi: https://doi.org/10.1101/202...

On 2021-06-01 14:16:32, user Bas Heijmans wrote:

Nice work, Roza and Anthony et al. We recently reported on TFs affecting DNAm in Genome Biol (https://genomebiology.biome.... Those were very much enriched for Zinc fingers (in particular with KRAB domain). Any overlap between your and our list? Or are our studies an example of the difference you will see when looking at different tissues and different 'developmental' stages? Will be interested to read your thoughts.

On 2021-05-11 00:22:05, user Jon wrote:

Interesting study. Klaus Kaestner group has recently published a paper describing the interaction of FOXA1 with demethylation pathways in a developmental context, the authors might want to cite and discuss it https://www.sciencedirect.c...

On 2021-06-01 06:06:21, user Prof. T. K. Wood wrote:

Unfortunately, much literature is missing from this manuscript:

Manuscript should cite the first persister proteome study; one that even used a similar technique, overproducing toxin YafQ (doi:10.1111/1462-2920.12567).

Manuscript should cite the first single cell work showing the importance of ribosomes and heterogeneity in persistence resuscitation (doi:10.1111/1462-2920.14093).

Manuscript should cite the first resuscitation study with single cells which showed the importance of HflX (https://doi.org/10.1016/j.i....

Manuscript should cite the persister formation work with single cells showing the importance of RaiA (https://doi.org/10.1016/j.b....

On 2021-05-31 11:32:09, user Gerhard WINGENDER wrote:

This study has been published: https://journals.plos.org/p...

On 2021-05-31 03:27:50, user zhentian kai wrote:

Excellent work!! Waiting for more technical details to be revealed

On 2021-05-30 18:00:44, user Adaobi Okafor wrote:

Hi, I have a question about which counts were used for clustering and DESeq2 analysis separately. It is stated that 2 different count data were generated ie read counts (from featureCounts), and TPM counts. I assume that read counts from featureCounts were used as input to DESeq2 while TPM counts were used as input into Clust. Is this correct? Thanks

On 2021-05-29 07:33:13, user Sjors Scheres wrote:

As laid out here (https://journals.iucr.org/d..., cryo-EM reconstructions of amyloids may suffer from local optima in the refinement that can lead to incorrect maps with seemingly decent (resolution) statistics. Maps with resolutions beyond 3.5 Å, in which continuous main-chain density with convincing side chains are resolved in all three directions, may provide increased confidence in the results.

Figure 1G, which does not show continuous main-chain density with convincing side chains, suggests that the quality of the cryo-EM structure presented in this preprint is of insufficient quality to propose a reliable atomic model. This observation is confirmed by our latest work (https://www.biorxiv.org/con..., which among various other diseases, describes cryo-EM structures of tau filaments from six cases of PSP. Our best PSP structure was calculated to a resolution of 2.7 Å and shows convincing main-chain and side-chain densities. Comparison of Figure 2A in this preprint with our structures suggests that although the overall shape of the fold is the same, approximately a third of the amino acids are modeled incorrectly, in particular in the stretches comprising residues 274-289, 324-337 and 366-375. Therefore, caution should be taken in the use of this structure for PET-ligand design, MD simulations, etc.

On 2021-05-29 03:00:00, user Iris Young wrote:

The preprint "Reciprocalspaceship: A Python Library for Crystallographic Data Analysis" describes a very welcome new lightweight tool for crystallographic data exploration and visualization. I'm excited about it for a number of reasons: it is intuitive and very quick to pick up, especially for users familiar with gemmi and pandas; it has documentation (!); it is a python3 library, with data objects interoperable with data visualization packages like matplotlib; and it is a permissively licensed, open-source package available on github. I can already imagine use cases for exploring unusual datasets in great depth.

My only suggestions for improvement of the reciprocalspaceship library itself are things it does not yet do, but very soon could. The ability to explore the raw data is extremely powerful. My most ambitious ask is a very simple GUI for direct visualization of reflections in reciprocal space, similar to the Phenix reciprocal space viewer. Other, smaller things could be less than a day's work: the tutorial walks through calculations such as CC1/2, which could easily be incorporated into the library's algorithms. I would suggest adding CC* as well for purposes of outlier detection, and for exploration of possible misindexing, a little more scaffolding could go a long way. (I am not sure what the "reindex" method does yet, which possibly already addresses this, as it is missing from the documentation.)

Regarding the preprint, it is an excellent introduction to the capabilities of the library. This is exactly what a preprint should be, and all the linked resources are in good shape for beta testing. I note some difficulties reading the equations, mainly due to a great number of variables that are never defined. I also encountered less common mathematical symbols (the delta-equal, which could be written out as a "let" statement), ambiguous ones (the hat on mu-hat), and notation that is simply visually dense (the use of overbars to denote means inside fractions, which might be alternatively denoted with angle brackets). With some attention to the equations, this will be a highly readable paper.

The process of reviewing this preprint has already given me enough of an opportunity to familiarize myself with reciprocalspaceship and to convince myself of its merits that I expect to be using it routinely from now on. Thank you to the developers for both the tool and the manuscript!

Minor points:<br /> - Figure 4 looks to be aggressively carved. The carving settings should be noted in the figure legend and should perhaps be a little more lenient in order to contextualize the size of the features shown, if this does not add excessive clutter.<br /> - The alpha parameter is mentioned in passing, with just enough detail to raise questions. Could this be expanded on just a bit?<br /> - PyMOL should be included in the references.<br /> - There is a typo in "The data [were] merged using Student's t-distributions"

Iris Young (Fraser Lab, UCSF)

On 2021-05-29 02:46:35, user Joshua Mylne wrote:

This has been peer reviewed and published in The Plant Cell "Structural and biochemical analyses of concanavalin A circular permutation by jack bean asparaginyl endopeptidase"<br /> https://doi.org/10.1101/202...

On 2021-05-29 00:30:09, user Devang Mehta wrote:

This preprint refers to Extended Data figures that have not been provided. There is also no Methods section, or text detailing the experimental methods and materials used.

On 2021-05-28 23:10:59, user Guido Petrovich wrote:

Line 748. It's Spf1. Beautiful work!

On 2021-05-28 18:28:26, user morgandjackson wrote:

Hi, I was keyed onto your recent in-press paper (Molecular Biology & Evolution) by a colleague and figured it would be prudent to leave a comment here regarding the status of your new species "Bombus incognitus". I'm not sure whether the intent was to describe "B. incognitus" as a new species or whether you're just using "Bombus incognitus" as a placeholder name for communication purposes as you continue to unravel the evolutionary patterns within the populations, but as it currently stands the name "Bombus incognitus" does not meet the requirements of the International Commission of Zoological Nomenclature (ICZN) and is thus not considered a valid species or available name yet. If the intent is to formally describe your cryptic population as a putative new species, I would recommend you become familiar with the requirements for doing so as outlined by the ICZN in The Code, particularly chapters 3 & 4 which detail the steps and requirements necessary to publish a new name that can be recognized officially. It may seem inane and inconsequential, but there remains the possibility that the organism you're referring to could be misconstrued by others or the name you've proposed replaced with something else entirely by someone else, creating a web of complications for future studies involving the taxa in question. Good luck.

On 2021-05-28 14:16:00, user Michael G LaMontagne wrote:

This paper is now published in PeerJ. https://peerj.com/articles/...

On 2021-05-28 07:44:25, user Huyen Thi Do wrote:

This is a valuable scientific research work, meticulously designed and obtained the novel, reliable results. The results of the work open up the research direction to search for substances that inhibit the pathogenicity of fungi Corynespora casiicola on rubber trees.

On 2021-05-27 18:13:47, user elisafadda wrote:

The following is my peer review. Again, congratulations to the authors on this great work.

"In this manuscript the authors present the results of an exceptional study of the deglycosylation of IgG Fc-glycans by<br /> Endo S2, generating and examining an impressive set of catalytically-competent complexes between an IgG Fc and Endo-S2. In this work, different molecular simulations approaches have been integrated harmoniously and performed successfully,<br /> in my opinion, to provide us with much needed insight into the Endo-S2 enzymatic activity. I truly enjoyed reading the manuscript and first and foremost would like to congratulate the authors on the work. I also would like to bring up the following few points and make some suggestions that the authors may find useful to consider and that I think may help bring the results<br /> together into a potential mechanism.

As the authors are aware, in isolated IgGs the two Fc-glycans are tightly packed within the Fc “horseshoe” structure, with each arm (considering complex N-glycans in human IgG1 for example)<br /> extending on either side of the Fc (see Harbison and Fadda, Glycobiology (2020) doi: https://doi.org/10.1093/gly....<br /> The crystal structure of the Endo-S2 in complex with the N-glycan was obtained with isolated N-glycans, i.e. not bound to the Fc. In view of this interactions, I believe, or as a general choice of strategy, molecular docking was used as the first step in making the models, by docking isolated N-glycans and then linking the Fc, if I understood correctly. Because the whole N-glycans<br /> do not extend at the sides of the Fc, so are not exposed, yet, as I mentioned earlier, extend across the Fc, I was wondering if the authors noticed in any of their simulations the interaction of only one of the arms on either glycans with the CBM that could potentially initiate extraction. More specifically, if the<br /> 1-6 on the CH2-CH3 side facing the domain interacts with the CBM, it could potentially trigger the opening/loosening of the Fc structure, increasing the accessibility to both glycans and promoting the binding of the whole glycan to the CBM and of the other glycan to the GH. This scenario would agree with model<br /> D, where the CBM acts as a ‘grip’ facilitating the removal of the opposite N-glycan by GH. The second deglycosylation event could occur according to model C, where the N-glycan bound to the CBM could be ‘transferred’ to the GH, which I found fascinating!

I understand that the above is a mechanistic speculation, yet a plausible one based on the evidence presented and in the literature, in my opinion, unifying all the different scenarios the<br /> authors examined and could be presented in the discussion. In any case, I think it would be useful to comment on how the N-glycans are potentially extracted from within the Fc to bind the CBM and GH.

As minor points,

I find that it would be really helpful to have Figures presenting the structures of the complexes in the main manuscript, indicating the positions/contacts of the glycans with CBM and GH in<br /> different models. Those could be integrated in Figure 1.

Page 10 and throughout<br /> “long-time” MD simulations is probably not a specific term, consider multi-microsecond MD simulations or MD simulations in the low microsecond time range.

Table 2 caption, “fist glycan” typo

Page 12, “S2A to D Fig.” probably better as “Fig. S2A to D.”

Figure 3 caption, the following sentence is unclear to me, please consider revising “Dashed lines indicate....”

Page 17, “an increase in ~400 Å” units needs to be<br /> squared.

On 2021-05-27 17:09:25, user Allan Konopka wrote:

I found this work via Antonia Fernandez-Garcia’s blog post from summer 2020, and thought it very intriguing. As I have a deep interest in physiological microbial ecology, I have wondered for some time now “whither metagenomics?” and this approach that categorizes GC’s by their “knownness” is helpful. Muren asked me to make further comment on a tweet (https://twitter.com/Hamatsa... <br /> here, to hopefully start a conversation.

So first, what is the objective of applying metagenomics? Sometimes stated (at least in grant proposals) is to “develop a predictive understanding of microbial communities.” But this implies knowing the function of the relevant gene products in adequate specificity (i.e., what specific biochemical function they carry out). We could all come up with lists of important functions, but let me identify 3 which I think are particularly problematic re: the databases of information.

1. Premise: the instantaneous activity rates of microbes are limited by the fluxes of an essential resource (for chemoheterotrophic bacteria, this is most often the diversity and concentrations of organic energy substrates)<br /> Inference: the breadth, levels of expression, and biochemical affinities of specific transport proteins are critical to understand interspecific competition in natural habitats.<br /> Problem: inadequate specificity – if “known” as (for example) an ABC transporter, this isn’t helpful in predicting in which cases a microbe has a selective advantage. [please correct me if there is recent work that improves this issue]

2. Premise: microbes/microbial communities rarely (if at all) exist in steady-state conditions. Rather, there are both regular and stochastic environmental perturbations to which organisms may evolve different strategies in response. [Side note: my fav paper on this is Nature’s Pulsing Paradigm, Estuaries 18: 547-555 (1995) by the three Odum brothers. Although about estuaries, easy to think how it applies to other systems and down to microscale.]<br /> Inference: Genes for regulation will be key here. <br /> Problem: I haven’t found much metagenomics work that addresses these regulatory proteins [please correct if necessary, as I have not done an exhaustive search of literature]. Likely (?) similar problem to transporters – motifs identifiable, but specificity of binding site unknown.<br /> Although most genome-scale simulation models (generally of one organism) generate a steady-state solution (and hence less useful ecologically), one can apply heuristics to simulate what you think you know re regulation (but this is outside metagenomics itself)

3. Premise: The extreme end of the “Pulsing Paradigm” are microbes in highly spatially structured habitats (soils, deep sediments, etc) in which the resource pulses are temporally rare<br /> Inference: evolutionary strategies that favor low/very low rates of metabolism (dormancy) better than the “optimistic” one high macromolecular content in terms of maintaining viability until the next pulse<br /> Problem: relatively weak understanding by microbial physiologists of dormancy (going beyond endospores)

On 2021-05-27 10:04:30, user Jan Nagel wrote:

We discussed your article in our journal club today and I thought we could briefly share some of our impressions with you.

We really liked your article and we think that the MycoLec database is a valuable tool for fungal research. <br /> We would like to suggest that the materials and methods be more descriptive especially regarding the scoring system. <br /> Figure 3 would be easier to interpret if some labels were added, eg. axis lables, labels indicating which column is the fold and class designation.<br /> You could also include a couple of sentences in the discussion regarding the limitations of this work, e.g. lack of experimentally validated domains across the fungal phylogeny decrease the power to detect all lectin domains.

Overall, we enjoyed reading and discussing your article and we hope it is published soon

On 2021-05-27 05:10:52, user BenjaminSchwessinger wrote:

I am<br /> reviewing this manuscript as part of the PCI Genomics initiative. I do apologize<br /> being late.

I think the<br /> overall conclusion of the manuscript are justified by the presented data that<br /> there are some structural variants between the assemblies and some changes in<br /> gene content.

I am<br /> confused about how candidate effectors were predicted and how CSEPs were<br /> analyzed as outlined below.

Major<br /> comments:

· <br /> I<br /> would suggest to tone down the claims on high quality DNA extraction for fungi<br /> and nanopore sequencing. The mean read length of 8Kb and N50 15.46kb are good<br /> but not outstanding for Nanopore, even for fungi. Also the 260/230 ratio of<br /> 1.45 does suggest residual polysaccharides in the DNA prep as this should be<br /> closer to 1.8. Plus there are several good fungal DNA extraction protocols<br /> available e.g. https://www.protocols.io/wo...<br /> and I would suggest the authors to add their protocol to the list.

· <br /> This<br /> study would benefit with comparison to the recent Stauber et al. work https://elifesciences.org/a....<br /> I presume the current strain would fall into clade CL3 of that paper. This other<br /> paper also compared strains against the Crouch et al. 2020 reference but with<br /> short reads only.

· <br /> Please<br /> explain the following: “EffectorP identified 1,117 models with a putative<br /> signal peptide,…pp.”. I don’t think effectorP predicts signal pepdites please clarify.<br /> This sections needs corrections as it is the wrong usage of EffectorP. EffectorP<br /> should only be applied on the secretome as mentioned in both original papers. This<br /> sections says there are 88 high confidence CSEPs. Latter analysis talks about<br /> effectors e.g S5 how are all these related?

· <br /> What<br /> is the pre-RIP index? I could not follow the following section:

o <br /> “Pre-RIP<br /> index was significantly higher than the estimated baseline frequency (1.28 in<br /> both the genomes, Figure 3B), suggesting the absence of a RIP signature. By<br /> contrast, estimates of the two post-RIP indexes for the four classes of TEs<br /> were either significantly higher or lower than the two estimated baseline<br /> frequencies (0.67 and 0.82 for TpA/ApT and CpG/GpC respectively, Figure 3B),<br /> suggesting a RIP activity for both the two genomes.”

o <br /> These<br /> two sentences appear to be contradictory to each other.

o <br /> I<br /> also did not follow the rational for using CpG/GpC for RIP analysis. Please explain.

Minor<br /> comments:

· <br /> Some<br /> of the citations in the literature in the introduction should be updated. E.g.<br /> there were several recent pan-genome papers e.g. tomato and soybean who looked<br /> at structural variation at the population level.

· <br /> The<br /> ‘two-speed genome hypothesis’ is only applicable to a subset of oomycete and<br /> fungal crop pathogens. There are many crop pathogens that do not show this<br /> compartmentalization including rust fungi and others. It would be good to see<br /> this reflected int the introduction.

· <br /> The<br /> DNA extraction protocol and especially the polysaccharide cleanup step is<br /> really interesting I would encourage the authors to post a detailed protocol at<br /> protocols.io https://www.protocols.io/wo...

· <br /> The<br /> genome assembly process seems a bit un-orthodox as they lack really good<br /> assemblers like Canu, Flye, or Masurca. I am also not convinced the Spades<br /> assembly is really the best as the differences in Illumina mapping rates,<br /> BUSCOs and Kmers is relatively small and would likely disappear with<br /> bootstrapping for these assemblies. Plus the high number of small might be a<br /> drawback of this assembly. Have the authors performed some quality control like<br /> BlobTools or such to see if these are spurious assemblies of bacterial contaminants?<br /> Just a minor comment. Also npScarf is really meant for simpler genomes like<br /> bacteria and not eukaryotes.

· <br /> Overall<br /> nicely curated assembly at the end.

On 2021-05-26 16:36:01, user Emily Gu wrote:

Hi, interesting work. I see you used ACT1 genes to normalize the rRNA expression in the transcriptome in four ploidy budding yeasts. But I wonder if you know if ACT1 expressed the same in different ploidy level yeasts? Eventhough it is the house keeping genes, but are there any upregulation or down regulation of this ACT1 genes in different ploidy? Or how you did the normalization?

On 2021-05-26 16:14:34, user Milka Kostić, PhD wrote:

Dear authors,

Thank you for sharing your preprint with the community. I enjoyed reading this manuscript and happy to share some thoughts below.

Kind regards,

Milka

GENERAL COMMENTS ON PREPRINT BY Frost, Rocha and Ciulli

In this preprint, Frost, Rocha and Ciulli report results of how cells respond to compounds previously described as inhibitors of von Hippel–Lindau (VHL) protein as measured by quantitative mass spectrometry (MS)-based proteomics. VHL is a well-studied protein that serves as a substrate recruiting/recognition subunit of Cullin RING E3 ligase CRL2VHL. The best characterized substrate of VHL is HIF1a, a hypoxia-inducible transcription factor that is under strict control of VHL and oxygen levels. Under normal oxygen conditions, HIF1a is hydroxylated on a proline residue and this modification enhances binding with VHL, resulting in HIF1a polyubiquitination and proteasomal degradation. However, under hypoxic conditions, which often occur in solid tumors, HIF1a is not hydroxylated and is therefore stabilized and able to up-regulate cancer-promoting gene transcription. However, in some conditions, upregulating HIF1a could be beneficial (if interested google Roxadustat). Therefore, agents that inhibit VHL-HIF1a complex formation under normoxic (normal O2) conditions emerged as of interest in drug discovery. Additionally, VHL is one of the most frequently hijacked E3 ubiquitin ligase in the context of targeted protein degradation and PROTAC (Proteolysis Targeting Chimera) development. Thus, VHL ligands are currently of very high interest.

The same lab has previously developed and characterized several VHL-HIF1a complex disruptors, including VH032 and VH298. Here, they take an important step to examine how these compounds affect cellular proteome. They also examine proteomic effects of proline hydroxylation (PHD) inhibitor (IOX2) - PHD is the enzyme that hydroxylates HIF1a under normoxic conditions - and benchmark everything against proteomic effects of hypoxia. The most interesting insight to emerge from these experiments is that treatment with VHL-HIF1a complex disruptors (aka inhibitors of Protein-Protein interactions (iPPIs)) leads to increase in levels of only two proteins: AMY1 (Amylase 1) and VHL. So, setting amylase aside, treatment with VHL “inhibitors” (more formally inhibitors of VHL-HIF1a binding) increases levels of VHL.

This is an unexpected and interesting finding, and the authors follow up to show that the effect is time-dependent, that the effects are at the level of protein not mRNA, that negative controls don’t have the same effect, and that this increase in VHL level is likely due to compound-induced increase in VHL protein stability. Importantly, the authors dive deeper into what happens to VHL ad HIF1a levels upon treatment with VH298, and how the effects change upon prolonged treatment and by increasing concentration of VH298.

The observations can be summarized as: it is complicated! More specifically:

Short treatment with VHL298 leads to disruption of VHL-HIF1a complex and increases levels of HIF1a (seen before and here)<br /> Prolonged treatment with VHL298 stabilizes VHL and increases VHL levels, and increased VHL level reduce HIF1a levels (seen here)<br /> Therefore, pharmacology of VHL ligands, even in the context of their use for PROTAC development may very well be complicated and future efforts would need to take this into account.

Overall, these are interesting results, and in my view the main implications of this work are importance of: (1) performing robust quantitative proteomics experiments as a part of validating/characterizing effects of small molecules; (2) not underestimating complexity of small molecule mechanism of action; and (3) accounting/examining potential differences of acute vs. prolonged treatments and acute vs. prolonged effects when characterizing and validating small molecules.

On 2021-05-26 15:25:12, user Nikolaos Sgourakis wrote:

Full article online at: <br /> https://www.nature.com/arti...

On 2021-05-26 09:25:39, user Kees Jalink wrote:

Addendum. On behalf of the crew: after submission, it was brought to our attention that reference 45, Burdyga et al, was inadvertently attributed to the Zaccolo lab. That should of course be the Lefkimmiatis lab. We apologize and will correct this mistake in a future version. Kees

On 2021-05-26 08:14:23, user Marcel Tarbier wrote:

This study is now published in Communications Biology: https://www.nature.com/arti...

On 2021-05-26 06:54:13, user Bastien Boussau wrote:

This manuscript has been recommended by PCI Evol Biol: https://evolbiol.peercommun...

On 2021-05-26 02:14:06, user ah3881 wrote:

The premise of this is wrong. It is not language barriers, it is international coordination and collaboration barriers. Any migratory species with a wide range will necessarily be challenging to conserve, transboundary and transnational collaboration is difficult. For marine wading species (i.e. the EAAF) some species show population declines of 79%, due to a loss of coastal wetland, much of this is Thai and Korean-but language is not the issue here (the value of the land is). I imagine if you looked at birds across the Americas, or Africa (shared languages) their threat would be soley due to value of prime habitats, and would not compare to language. Furthermore, even across areas like Central Asia (where Russian is a shared language) political barriers will continue to be the prime barrier, not language. Other factors need to be explored in this context, it does not collapse down to language

On 2021-05-25 15:41:08, user Ian Hastings wrote:

I have two major comments on this preprint.

Firstly, the conclusions are not novel but echo those we previously reported several years ago from similar pharmacological considerations [1] i.e. that selection against ACTs will likely occur in two phases i.e. “Phase 1 is characterised by resistance eroding the therapeutic capacity of the partner drug…….. Phase 2 then starts because both the artemisinin and partner drugs have similar therapeutic capacities so both contribute to cure and hence selection pressure exists for resistance to each drug”. The current preprint essentially repeats this and demonstrates that the more phase 1 has progressed, the faster phase 2 proceed, see their abstract i.e “Higher frequencies of pre-existing partner-drug resistant genotypes lead to earlier establishment of artemisinin resistance”. This is the same conclusion we reached previously i.e. we stated “The main threat to antimalarial drug effectiveness and control comes from resistance evolving to the partner drugs”. I made the corresponding author aware of our previous work [1] and it is disappointing that they choose not to make this previous work available to readers, nor to interpret there results within this context. In fact, the very title of the preprint states it is rediscovering our Phase 2. Two publication reaching the same conclusion are obviously more compelling than one, hence the need to cross-cite

Secondly, they have modelled three partner drugs: amodiaquine (AQ), piperaquine (PPQ) and lumefantrine (LF). It is important to note their modelling differs from the real drugs’ pharmacology in some key respects. Their parametrisation assumes one-compartment (1-c) pharmacokinetics for all drugs and calibration between drugs differs solely in their half-lives and maximum killing rates; EC50 values are selected to obtain their chosen failure rates and resistance mutations affect IC50. In reality, PPQ and LF follow 2- or 3- compartment pharmacokinetics (depending on the source publication) while AQ is even more complex (it is converted to its active metabolite DEAQ and both AQ and DEAQ have antimalarial activity and 2 compartment pharmacokinetics). The calibrations are in arbitrary units (e.g. dosage per patient in mg/Kg are not given); compare this to, for example, the extensive pharmacological calibrations tabulated in [2]. The pharmacological details are not obvious in the preprint. They cite their ref #17, but this back-cites to the SI of a previous paper [3]. Essentially ,they use 3 different calibration of a 1-compartment drug. There is nothing inherently wrong in using a PK approximation using simple 1-c dynamics provided this is clearly stated. However, calling them PPQ, LF and AQ without making this clear gives an aura of pharmacological accuracy and precision which is simply not present in their models. This is a vital caveat given recent realisation that the evolution of drug resistance needs to be placed firmly within its pharmacological context (e.g. discussed in these reviews [2, 4]).<br /> There is nothing inherently wrong in this work, it is essentially a question of transparency i.e. (1) to acknowledge previous work and that their results are consistent with previous analyses rather than being novel (2) to provide explicit description and discussion of their pharmacological models of specific antimalaria drugs.

Ian Hastings, Liverpool School of Tropical Medicine.

1. Hastings IM, Hodel EM, Kay K. Quantifying the pharmacology of antimalarial drug combination therapy. Scientific Reports 2016; 6:32762.
2. Zaloumis S, Humberstone A, Charman S, et al. Assessing the utility of an anti-malarial pharmacokinetic-pharmacodynamic model for aiding drug clinical development. Malaria J 2012; 11:303.
3. Nguyen TD, Olliaro P, Dondorp AM, et al. Optimum population-level use of artemisinin combination therapies: a modelling study. The Lancet Global Health 2015; 3:e758-e66.
4. Simpson JA, Zaloumis S, DeLivera AM, Price RN, McCaw JM. Making the Most of Clinical Data: Reviewing the Role of Pharmacokinetic-Pharmacodynamic Models of Anti-malarial Drugs. The AAPS Journal 2014.

On 2021-05-25 09:23:40, user 1234 wrote:

The authors have done a great job attempting to improve antigen epitopes identification. But there are minor issues with the paper in the present form.<br /> "Experimental methods, such as X-ray crystallography, nuclear magnetic resonance and phage display" I would suggest the author to add comma " Experimental methods, such as X-ray crystallography, nuclear magnetic resonance, and phage display"<br /> "the averaged RMSD (root mean square deviation) of the atoms between the two structures is 0.434 ± 0.636Å, while the RMSD of the atoms at the epitope region is 0.576 ± 0.748Å". Please include comparison reference, Z-scors as well as number of compared residues in epitope region.<br /> "For instance, Alanine has no torsion angle, while Proline has five torsion angles" add residue to Alanine and Proline

On 2021-05-21 06:41:46, user bilogo wrote:

Flexibility is a simple but useful,novel concept.A simple change can improve performance so much.This study will give researchers new insights into epitope prediction.

On 2021-05-19 08:08:09, user disqus_1DLwDcoOSV wrote:

Protein flexibility has been widely studied, but few studies link it to epitope prediction. This study that applies the flexibility to epitope prediction pioneers new ideas for epitope prediction and even protein interactions research.

On 2021-05-25 02:48:35, user Zhixing Feng wrote:

This paper is accepted by Nature Communications. The latest version is available at <br /> https://doi.org/10.1038/s41...

On 2021-05-24 23:07:50, user Denise Arico wrote:

It is striking how polarized cell growth has arisen in sessile organisms across independent evolution pathways. There are several examples such as pollen tube and root hair in higher plants, moss and fern protonemata, fungal hyphae and some brown algae embryos. What fascinates me more is the fact that different highly-controlled mechanisms lead to similar physical properties which allow this type of intricated cell growth. For instance, pollen tube growth involves tight coordination of reactive oxygen species, a Ca2+ gradient and a high traffic of vesicles to the pollen tube tip with a constant remodelling of the cell wall. Indeed, the integrity of the pollen tube during polarized growth is maintained by an autocrine signalling in which certain RALF peptides are secreted to the apoplast where they interact with specific Extensins that participate in cell wall assembly. The lack of pollen Extensins produces abnormal cell walls (with altered levels of pectin/callose components) causing a complete shutdown of the polar growth and pollen tube bursting (reviewed in Sede et.al, 2018; Somoza et.al., 2020). This work of yours began to elucidate the wall-driven cellular expansion mechanisms in brown algae. I imagine it has been really challenging to work on the transcriptomics of Fucus embryo development and assemble Fucus genome. Since the lack of molecular genetic tools in brown algae is a clear limitation, I wonder if a UV mutagenesis screen on Fuscus embryos can identify mutants that fail to develop tallus or rhizoid properly so as to go on elucidating the signaling pathways. This approach was performed in Ectocarpus (Godfroy et.al., 2017). Also, combining assays using for example 2,7-dichlorofluorescein diacetate probe (H2DCF-DA) to analyze ROS levels, Ca2+ chelators, Brefeldin A to disrupt Golgi, and inhibitors of proline hydroxylation (preventing o-glycosylation of AGPs), may help characterize rhizoid elongation.<br /> Since I’m more familiar with cortical microtubules in epidermal cells of dark-grown hypocotyls, it blows my mind the fact that brown algae lack cortical microtubules. So, actin filaments play a preponderant role in orientating cellulose microfibrils (Katsaros et.al., 2006); contrary to what has been observed in higher plant cells where cortical microtubules are mainly involved in cell wall morphogenesis. I wonder if actin filaments have any adaptive advantage over cortical microtubules in coping with tension forces that might arise from the osmotic status adjustment to seawater. Or if cell wall physical properties from algae are more suitable for dealing with seawater osmotic challenge. It seems reading your preprint provoked me a little brainstorming!

On 2021-05-24 22:36:53, user Howard Salis wrote:

Readers note: The authors make the following assumptions in all their analysis, which critically undermines several of their most important (and controversial) conclusions:

1. The authors are treating their ribosome profiling experiments as a measurement of translation rate. That's incorrect. Ribosome profiling measures the relative density of ribosomes bound to mRNAs. It is not a direct measurement of translation rate nor is it a direct measurement of translational efficiency.

Let me be clear with these terms: Translation rate is the number of proteins produced per mRNA per time. Translational efficiency is the number of proteins produced by a single transcript before it is degraded. Ribosome density is the translation initiation rate divided by the mRNA's translation elongation rate.

1. The authors assume that all mRNAs have the same translation elongation rate in order to convert ribosome densities into translation rates. For example, in their Equation 5, epsilon (translation elongation rate) is just a single constant, used throughout to relate translation rates to protein synthesis rates and protein concentrations. This is incorrect. mRNAs do not all have the same translation elongation rate. There is a whole genre of literature on synonymous codon usage, the effects of synonymous codons on ribosome translocation speeds, and the use of codon optimization to increase heterologous protein expression levels. Epsilon is not a single constant. At the very least, if we only care about protein concentrations, one must consider the CDS-averaged translation elongation rate for each mRNA transcript in the transcriptome.

The authors' conclusion "Translation initiation rates are similar across mRNAs and growth conditions" needs to be revisited without assuming that all translation elongation rates are the same. Likewise, the conclusion that "Total mRNA abundance matches the translational capacity" depends on the veracity of this conclusion. The conclusion that "Constancy of ribosome spacing across mRNA and nutrient conditions" is more accurately viewed as "Constancy of *ribosome density* across mRNA and nutrient conditions". Finally, the conclusion that "Total mRNA synthesis flux is adjusted to match translational capacity" is again dependent on the veracity of the first conclusion.

Concluding that all mRNAs have the same translation rate is bold. But it's not supported by data. If you see someone using ribosome profiling to make this claim, be skeptical!

On 2021-05-23 15:40:50, user michael_in_adelaide wrote:

This paper has now been published in the Journal of Alzheimer's Disease: https://content.iospress.co...

On 2021-05-23 15:38:01, user michael_in_adelaide wrote:

This paper has now been published in Journal of Alzheimer's Disease Reports: https://content.iospress.co...

On 2021-05-23 09:19:53, user Tal Shay wrote:

Finally out in https://academic.oup.com/na...

On 2021-05-23 09:18:59, user Tal Shay wrote:

We apologize for not citing Digger (Louadi et al. Nucleic Acids Research, 2020), which allows studying the functional effect of alternative splicing on protein -protein interactions and domain-domain interactions - check it out and compare at https://exbio.wzw.tum.de/di...

On 2021-05-22 12:48:46, user Prof. T. K. Wood wrote:

1. Fig. 4 shows indole-treated cells are not persisters (cells dying rapidly) so there are little data showing difference in energy states in dormant bacteria.
2. What solvent was used for indole? Note the extraordinary high conc (10 mM) used. No solvent controls shown.
3. Indole is not a "putative" signal. Refs missing for indole as a intra-species (Rather's group), inter-species (Wood group), and interkingdom signal (Wood group).
4. Cm to cease protein protein and make persisters is same as Tet pretreatment already published but not cited (see doi doi:10.1128/AAC.02135-12, 2013).

On 2021-05-22 09:29:43, user Tom Jacobs wrote:

Why use a gateway cloning reaction at the end? It is more straightforward to do a golden gate reaction into the final vector, not an intermediate.

On 2021-05-21 16:36:41, user Jack Stevenson wrote:

Summary:<br /> tRNAs are heavily chemically modified in human and other cells by a variety of enzymes to facilitate their proper folding and function. Lentini et al. report their investigation of a previously undescribed role for the tRNA cytosine methyltransferase homolog METTL8 as the enzyme responsible for the 3-methylcytosine modification on the anticodon loop of human mitochondrial tRNAs.

The authors aim to demonstrate: 1. that METTL8 is localized to mitochondria, 2. that METTL8 physically associates with mt-Ser and -Thr tRNAs as well as mitochondrial seryl-tRNA synthetase, 3. that mitochondrially-localized METTL8 is necessary for m3C modification of those same tRNAs and 4. that METTL8-mediated modification of mt-Ser tRNA affects the tRNA’s structure.

They succeed in demonstrating each of these points in a clear and straightforward manuscript, advancing the field’s knowledge of tRNA modification with the novel finding that m3C modification can affect tRNA structure and by assigning the role of mitochondrial m3C modification to METTL8.

Their METTL8 knockout and rescue experiments are particularly convincing, showing that METTL8 knockout cells lack modification of mt-Ser and -Thr tRNAs and that expression of METTL8 but not METTL8-ΔMTS rescues modification. This is strong evidence in support of their conclusion that METTL8 is necessary and likely directly responsible for m3C modification of those tRNAs. They likewise demonstrate that METTL8 but not METTL8-∆MTS rescues a defect in mt-tRNA-Ser structure. The text is appropriately cautious in interpreting the possible mechanisms behind this observation, but it is undoubtedly interesting and points to an important role for METTL8 in regulation of at least mt-tRNA-Ser and possibly others.

Major points:<br /> To identify RNA gel bands as specific RNA binding partners of METTL8 the authors rely on Northern blotting, taking advantage of the fact that this technique can specifically identify species of RNA suspected to be present. They admirably state a specific and limited conclusion from this experiment: “...a subpopulation of METTL8 is imported into mitochondria where it interacts with mitochondrial tRNAs containing the m3C modification.” However, an additional conclusion is implied by the results presented, though the authors correctly choose not to emphasize it: that METTL8 interacts only with m3C-modified mt-tRNAs and not with non-m3C-modified mt-tRNAs or m3C-modified nuclear tRNAs. This is a potentially interesting finding, but the authors only test a single mt-tRNA (mt-tRNA-Ile) besides the two already thought to be m3C-modified, and no nuclear tRNAs for AAs besides Ser and Thr, so the finding is not very strongly supported. It might be a straightforward and interesting followup experiment to blot for a larger panel of tRNAs to lend stronger support to this conclusion and allow it to be emphasized as another significant finding.

To demonstrate that the described novel functions of METTL8 depend on its mitochondrial localization, the authors rely on a METTL8-ΔMT construct lacking a mitochondrial targeting sequence, observing repeatedly that the ΔMT construct fails to rescue phenotypes that are rescued by wild-type METTL8. One unlikely but potentially serious issue, however, is that the authors do not demonstrate that their METTL8-ΔMTS construct retains activity. A loss of activity could also explain the observed result (the construct’s failure to rescue mt-Ser and -Thr-tRNA modification) as well as loss of mitochondrial localization can. The authors should note this potential mechanism in the text. They might consider testing METTL8-ΔMT activity as further validation, though lack of this validation does not cast serious doubt on their conclusions.

Minor points:<br /> -The MitoFates algorithm should be described in somewhat more detail in the text to clarify what qualities of the METTL8 sequence contributed to the algorithm’s prediction that METTL8 is localized to mitochondria. Does the algorithm consider the MPP site as well as the MTS? Does it also consider the TOM20 sites, or were those only noted after the fact?

-Figure 3 lettering should be reordered to read from top to bottom.

-The PHA quantification presented in the figures is confusing. The paper defines the PHA number presented as “the ratio of PHA versus control probe signal expressed relative to the WT1 cell line.” But it seems that a more relevant metric for interpreting these blots for the effect of METTL8 on a given tRNA would be a ratio of ratios: the ratio of KO to WT PHA bands compared to the ratio of KO to WT control bands. METTL8 modifies a particular tRNA if the ratio of KO to WT PHA signal is much higher than the ratio of KO to WT control signal, as is clearly the case for e.g. mt-tRNA-Ser-UGA WT2 and KO2. An explanation of the quantification would be a nice addition to the figure legend, or the quantification could be changed to another metric like the one proposed above.

-Figure S4 uses a nonspecific antibody band as loading control rather than a housekeeping protein. This is unusual, and it would be useful if the authors could comment on this choice.

On the whole, the methods section is relatively detailed and thorough, which is great for making the experiments described reproducible, but a little more detail would ensure reproducibility further. In particular:<br /> -Sequences should be provided for all constructs used in the paper. It is technically possible to deduce the sequences of the constructs from the provided primers, but construct sequences would make it easier for readers to understand and evaluate the work.<br /> -The authors report having verified construct expression by immunoblotting; it would be useful for this existing data to be included in the supplement.<br /> -Catalog numbers should be provided for all reagents and kits used to aid in reproducibility. For instance, “cells were...harvested for DNA extraction (Qiagen)” is not sufficient for an interested scientist to replicate the work. Likewise, more complete conditions or references should be provided for protocols: for instance, gel transfer times, buffers and voltages are not provided, and blot detection procedures are not fully described, including secondary antibodies/detection reagents and imaging methods. More experimental details would make this heavily blot-based paper stronger.<br /> -To forestall any confusion about off-target or unexpected bands and to fall in line with best practices for blot-based assays, it would be good for full blots to be included in the supplement for all partial blots shown in the figures.

-The references “Zhang 2020a” and “Zhang 2020b” seem to be reversed—the manuscript refers to “2020a,” but in the context of the topic of 2020b, on pages 6 and 7.

-The authors are recognized for submitting what must be the only paper on BioRxiv in 2021 so far to investigate SARS2 but not COVID-19.

Reviewed by Jack Stevenson as part of the UCSF Peer Review minicourse with James Fraser

On 2021-05-21 14:14:59, user R Greg Thorn wrote:

Nice work and potentially an important concept in invasion biology, but please clarify the identification step of your bioinformatics pipeline. An approximate match in QIIME/UNITE is not an identification. Talaromyces marneffei is (we hope!) unlikely to be a common fungus in Illinois soils. It is a serious human pathogen that is, so far as we know, restricted to southeast Asia, centered on Laos, Cambodia and Vietnam. Some other IDs are equally suspect. Please don't let this get into print.

On 2021-05-21 06:01:38, user Victor Lopez del Amo wrote:

This manuscript was published in Nature Communications:

https://www.nature.com/arti...

On 2021-05-20 22:19:49, user 崖の上の生命科学DB流通業者 wrote:

This manuscript was peer reviewed and published in Biomedicines. <br /> https://doi.org/10.3390/bio...