I actually think that the tweets coming from Trump himself in this context are MORE authentic than the ones coming from his campaign team. As users of the platform and people living in this country, we expect a certain flavor of content out of Trump's tweets. Seeing posts from his campaign next to posts from Trump in some ways acts to muddy the waters. If the public face of a presidential candidate was always angry and negative, many voters may be turned away from that candidate. But by intermixing calm, structured posts, it makes the candidate appear able to switch their anger and negativity on and off. Which may be more appealing to voters.

Author response:

General Statements

We thank the reviewers for their insightful and constructive comments, which have substantially strengthened the manuscript. We have addressed all concerns and replaced the previous nonquantitative RNA-seq analysis with a new analysis that allowed for quantitative assessment. We were encouraged to find that the revised analysis not only confirmed our original observations but also reinforced and extended our conclusions.

Point-by-point description of the revisions

Reviewer #1:

Significance

At its current stage, this work represents a robust resource for molecular parasitology research programs, paving the way for mechanistic studies on multilayered gene expression control and it would benefit from experimental evidence for some of the claims concerning the in silico regulatory networks. Terms like "regulons", "recursive feedback loop" are employed without solid confirmation or extensive literature support. In my view, the most relevant contribution of this study is centered in the direct association between proteasome-dependent degradation and Leishmania differentiation.

We thank the reviewer to acknowledge the impact of our work as a robust resource for further mechanistic studies. We agree that the new concepts emerging from our multilayered analysis should be experimentally assessed. However, given the scope of our analysis (i.e. a complete systems-level analysis of bona fide, hamster-isolated L. donovani amastigotes and derived promastigotes) and the amount of data presented in the current manuscript, such functional genetic analysis will merit an independent, in-depth investigation. The current version has been very much toned down and modified to emphasize the impact of our work as a powerful new resource for downstream functional analyses.  

Evidence, reproducibility and clarity

The narrative becomes somewhat diffuse with the shift to putative multilevel regulatory networks, which would benefit from further experimental validation.

We agree with the reviewer and toned down the general discussion while suggesting putative multilevel regulatory networks for follow-up, mechanistic analyses. We now emphasize those networks for which evidence in trypanosomatids and other organisms has been published. Experimental validation of some of these regulatory networks is outside the scope of our manuscript and will be pursued as part of independent investigations.

Major issues

Fig.1D suggests a significant portion of the SNPs are exclusive, with a frequency of zero in one of the two stages. Were only the heterozygous and minor alleles plotted in Fig.1D, since frequencies close to 1 are barely observed? Is the same true in Sup Fig. S2B? Why do chrs 4 and 33 show unusual patterns in S2B?

We thank the reviewer for this observation. The SNPs exclusive to either one or the other stage are likely the result of the 10% cutoff we use for this kind of analysis (eliminating SNPs that lack sufficient support, i.e. less than 10 reads). Due to bottle neck events (such as in vitro culture or stage differentiation), many low frequency SNPs are either ‘lost’ (filtered out) or ‘gained’ (passing the 10% cutoff) between the ama and pro samples. All SNPs above 10% were plotted. The absence of SNPs at 100% is one of the hallmarks of the Ld1S L. donovani strain we are using. Instead, these parasites show a majority of SNPs at a frequency of around 50%, which is likely a sign of a previous hybridization event. Chr 4 and chr 33 show a very low SNP density, most likely as they went through a transient monosomy at one moment of their evolutionary history, causing loss of heterozygosity. We now explain these facts in the figure legend.

Chr26 revealed a striking contrasting gene coverage between H-1 and the other two samples. While a peak is observed for H-1 in the middle of this chr, the other two show a decrease in coverage. Is there any correlation with the transcriptomic/proteomic findings?

This analysis is based on normalized median read depth, taking somy variations into account. This is now more clearly specified in the figure legend. We do not see any significant expression changes that would correlate with the observed (minor) read depth changes. As indicated in the legend, we do not consider such small fluctuations (less than +/- 1,5 fold) as significant. The reversal of the signal for chr 26 sample H1 eludes us (but again, these fluctuations are minor and not observed at mRNA level).

The term "regulon" is used somewhat loosely in many parts of the text. Evidence of co-transcriptomic patterns alone does not necessarily demonstrate control by a common regulator (e.g., RNA-binding protein), and therefore does not fulfill the strict definition of a regulon. It should be clear whether the authors are highlighting potential multiple inferred regulons within a list of genes or not. Maybe functional/ gene module/cluster would be more appropriate terms.

We thank the reviewer for this important comment. We replaced ‘regulon’ throughout the manuscript by ‘co-regulated, functional gene clusters’ (or similar).

It is unclear whether the findings in Fig.3E are based on previous analysis of stagespecific rRNA modifications or inferred from the pre-snoRNA transcriptomic data in the current work or something else. I struggle to find the significance of presenting this here.

We thank the reviewer for this comment. Yes, these data show stage-specific rRNA modifications based on previous analyses that mapped stage-specific differences of pseudouridine (Y) (Rajan et al., Cell Reports 2023, DOI: 10.1016/j.celrep.2024.114203) and 2'O-modifications (Rajan et al., Nature Com, in revision) by various RNA-seq analyses and cryoEM. This figure has been modified in the revised version to consider the identification of stageregulated snoRNAs in our new and statistically robust RNA-seq analysis. These data are shown to further support the existence of stage-regulated ribosomes that may control mRNA translatability, as suggested by the enriched GO terms ‘ribosome biogenesis’, ‘rRNA processing’ and ‘RNA methylation’ shown in Figure 2. We better integrated these analyses by moving the panels from Figure 3 to Figure 2.

The protein turnover analysis is missing the critical confirmation of the expected lactacystin activity on the proteasome in both ama and pro. A straightforward experiment would be an anti-polyUb western blotting using a low concentration SDS-PAGE or a proteasome activity assay on total extracts.

We thank the reviewer for this comment and have now included an anti-polyUb Western blot analysis (see Fig S7).

The viability tests upon lactacystin treatment need a positive control for the PI and the YoPro staining (i.e., permeabilized or heat-killed promastigotes).

This control is now included in Fig S7 and we have added the corresponding description to the text.

I found that the section on regulatory networks was somewhat speculative and less focused. Several of the associated conclusions are, in some parts, overstated, such as in "uncovered a similar recursive feedback loop" (line 566) or "unprecedented insight into the regulatory landscape" (line 643). It would be important to provide some form of direct evidence supporting a functional connection between phosphorylation/ubiquitination, ribosome biogenesis/proteins and gene expression regulation.

We agree with the reviewer and have considerably toned down our statements. Functional analyses to investigate and validate some of the shown network interactions are planned for the near future and will be published separately.

Minor issues

(1) The ordinal transition words "First,"/"Second," are used too frequently in explanatory sections. I noted six instances. I suggest replacing or rephrasing some to improve flow.

Rectified, thanks for pointing this out.

(2) Ln 168: Unformatted citations were given for the Python packages used in the study.

Rectified, thanks for pointing this out.

(3) Fig.1D: "SNP frequency" is the preferred term in English.

Corrected.

(4) Fig.2A: not sure what "counts}1" mean.

This figure has been replaced.

(5) Ln 685: "Transcripts with FC < 2 and adjusted p-value > 0.01 are represented by black dots" > This sentence is inaccurate. The intended wording might be: "Transcripts with FC < 2 OR adjusted p-value > 0.01 are represented by black dots"

We thank the reviewer and corrected accordingly.  

(6) Ln 698: Same as ln 685 mentioned above.

We thank the reviewer and corrected accordingly.

(7) Fig.2B and elsewhere: The legend key for the GO term enrichment is a bit confusing. It seems like the color scales represent the adj. p-values, but the legend keys read "Cluster efficiency" and "Enrichment score", while those values are actually represented by each bar length. Does light blue correspond to a max value of 0.05 in one scale, and dark blue to a max value of 10-7 in the other scale?

This was corrected in the figure and the legends were updated accordingly.

(8) Sup Figure S3A and S4A: The hierarchical clustering dendrograms are barely visible in the heatmaps.

Thanks for the comment. Figure S3 was removed and replaced by a hierarchical clustering and a PCA plot.

(9) S3A Legend: The following sentence sounds a bit awkward: "Rows and columns have been re-ordered thanks to a hierarchical clustering". I suggest switching "thanks to a hierarchical clustering" to "based on hierarchical clustering".

This figure was removed and the legend modified.

(10) Fig.5D: The font size everywhere except the legend key is too small. In addition, on the left panel, gene product names are given as a column, while on the right, the names are shown below the GeneIDs. Consistency would make it clearer.

Thank you, this is now rectified. To ensue readability, we reduced the number of shown protein kinase examples.

Reviewer #2 Evidence, reproducibility and clarity:

In the absence of riboprofiling the authors return to the RNA-seq to assess the levels of pre-Sno RNA (the role of the could be more explicitly stated).

We thank the reviewer for this comment. We moved the snoRNA analysis from Fig 3 to Fig 2 (see also the similar comment of reviewer 1), which better integrates and justifies this analysis. Based on the new and statistically robust RNA-seq analysis, the volcano plot showing differential snoRNA expression and possible ribosome modification has been adjusted (Figures 2C and D).

The authors provide a clear and comprehensive description of the data at each stage of the results and this in woven together in the discussion allowing hypotheses to be formed on the potential regulatory and signalling pathways that control the differentiation of amastigotes to promastigotes. Given the amount and breadth of data presented the authors are able to present a high-level assessment of the processes that form feedback loops and/or intersectional signalling, but specific examples are not picked out for deeper validation or exploration.

We thank the reviewer to acknowledge the amount and breadth of data presented. As indicated above (see responses to reviewer 1), mechanistic studies will be conducted in the near future to validate some of the regulatory interactions. These will be subject of separate publications. As noted above (response to reviewer 1), we toned down the general discussion, suggest follow-up mechanistic analyses and emphasize those networks for which evidence in trypanosomatids and other organisms has been published.

Major comments:

(1) As I have understood it from the description in the text, and in Data Table 4, the RNA-seq element of the work has only been conducted using two replicates. If this is the case, it would substantially undermine the RNA-seq and the inferences drawn from it. Minimum replicates required for inferential analysis is 3 bio-replicates and potentially up to 6 or 12. It may be necessary for the authors to repeat this for the RNA-seq to carry enough weight to support their arguments. (PMID: 27022035)

We agree with the reviewer and conducted a new RNA-seq analysis with 4 independent biological replicates of spleen-purified amastigotes and derived promastigotes. Given the robustness of the stage-specific transcriptome, and the legal constrains associated with the use of animals, we chose to limit the number of replicates to the necessary. We thank the reviewer for this important comment, and the new data not only confirm the previous one (providing a high level of robustness to our data) but allowed us to increase the number of identified stage-regulated snoRNAs, thus further supporting a possible role of ribosome modification in Leishmania stage development.   

(2) There are several examples that are given as reciprocal or recursive signalling pathways, but these are not followed up with independent, orthogonal techniques. I think the paper currently forms a great resource to pursue these interesting signalling interactions and is certainly more than just a catalogue of modifications, but to take it to the next level ideally a novel signalling interaction would be demonstrated using an orthogonal approach. Perhaps the regulation of the ribosomes could have been explored further (same teams recently published related work on this). Or perhaps more interestingly, a novel target(s) from the ubiquitinated protein kinases could have been explored further; for example making precision mutants that lack the ubiquitination or phosphorylation sites - does this abrogate differentiation?

We agree with the reviewer that the paper currently forms a great resource. In-depth molecular analysis investigating key signaling pathways and regulatory interactions are outside the scope of the current multilevel systems analysis but will be pursued in independent investigations.

(3) I found the use of lactacystin a bit curious as there are more potent and specific inhibitors of Leishmania proteasomes e.g. LXE-408. This could be clarified in the write-up (See below).

We thank the reviewer for this comment. We opted for the highly specific and irreversible proteasome inhibitor lactacystin that has been previously applied to study the Leishmania proteasome (PMID: 15234661) rather than the typanosomatid-specific drug candidate LXE408 as the strong cytotoxic effect of the latter makes it difficult to distinguish between direct effects on protein turnover and secondary effects resulting from cell death, limiting its utility for dissecting proteasome function in living parasites. We have added this information in the Results section.

(4) If it is the case that only 2 replicates of the RNA-Seq have been performed it really is not the accepted level of replication for the field. Most studies use a minimum of 3 bioreplicates and even a minimum of 6 is recommended by independent assessment of DESeq2.

See response to comment 1 above.

(5) As far as I could see, the cell viability assay does not include a positive control that shows it is capable of detecting cytotoxic effects of inhibitors. Add treatment showing that it can differentiate cytostatic vs cytotoxic compound.

This control has now been added to Fig S7.

(6) It is realistic for the authors to validate the cell viability assay. If the RNA-seq needs to be repeated then this would be a substantial involvement.

Redoing the RNA-seq analysis was entirely feasible and very much improved the robustness of our results.

(7) All the methods are written to a good level of detail. The sample prep, acquisition and data analysis of the protein mass spectrometry contained a high level of detail in a supplemental section. The authors should be more explicit about the amount of replication at each stage, as in parts of the manuscript this was quite unclear.

We thank the reviewer for this comment and explicitly state the number of replicates in Methods, Results and Figure legends for all analyses. The number of replicates for each analysis is further shown in the overview Figure S1.

(8) Unless I have misunderstood the manuscript, I believe the RNA-seq dataset is underpowered according to the number of replicates the authors report in the text.

See response to comment 1 above.

(9) Looking at Figure 1 and S1 and Data Table 4 to show the sample workflow I was surprised to see that the RNA-seq only used 2 replicates. The authors do show concordance between the individual biological replicates, but I would consider that only having 2 is problematic here, especially given the importance placed on the mRNA levels and linkage in this study. This would constitute a major weakness of the study, given that it is the basis for a crucial comparison between the RNA and protein levels.

We agree and have repeated the RNAseq analysis using four independent biological replicates - see response to comment 1.

(10) It also wasn't clear to me how many replicates were performed at each condition for the lactacystin treatment experiment - can the authors please state this clearly in the text, it looks like 4 replicates from Figure S1 and Data Table 8.

Indeed, we did 4 replicates. This is now clarified in Methods, Results and Figure legends and shown in Figure S1.

(11) Four replicates are used for the phosphoproteomics data set, which is probably ok, but other researchers have used a minimum of 5 in phosphoproteomics experiments to deal with the high level of variability that can often be observed with low abundance proteins & modifications. The method for the phosphoproteomics analysis suggests that a detection of a phosphosite in 1 sample (also with a localisation probability of >0.75) was required for then using missing value imputation of other samples. This seems like a low threshold for inclusion of that phosphosite for further relative quantitative analysis. For example, Geoghegan et al (2022) (PMID: 36437406) used a much more stringent threshold of greater than or equal to 2 missing values from 5 replicates as an exclusion criteria for detected phoshopeptides. Please correct me if I misunderstood the data processing, but as it stands the imputation of so many missing values (potentially 3 of 4 per sample category) could be reducing the quality of this analysis.

We thank the reviewer for this remark and for highlighting best practices in phosphoproteomics data analysis. Unlike other studies that use cultured parasites and thus have access to unlimited amounts, our study employs bona fide amastigotes isolated from infected hamster spleens. In France, the use of animals is tightly controlled and only the minimal number of animals to obtain statistically significant results is tolerated (and necessary to obtain permission to conduct animal experiments).

Regarding the number of biological replicates, we would like to emphasize that the use of four biological replicates is fully acceptable and used in quantitative proteomics and phosphoproteomics, particularly when combined with high-quality LC–MS/MS data and stringent peptide-level filtering. While some studies indeed employ five or more replicates, this is not a strict requirement, and many high-impact phosphoproteomics studies have successfully relied on four replicates when experimental quality and depth are high. In the present study, we adopted a discovery-oriented approach, aimed at detecting as many confidently identified phosphopeptides as possible. The consistency between replicates, combined with the depth of coverage and signal quality, indicates that four replicates are adequate for both the global proteome and the phosphoproteome in this context. Importantly, the quality of the MS data in this study is supported by (i) a high number of confidently identified peptides and phosphopeptides (identification FDR<1%), (ii) robust phosphosite localisation probabilities (localisation probability >0.75), and (iii) reproducible quantitative profiles across replicates. Notably, most of the identified phosphopeptides are quantified in at least two replicates within a given condition (between 73.2% and 83.4% of all the identified phosphopeptides among replicates of the same condition).

Regarding missing value imputation, we appreciate that our initial description may have been unclear and we have revised the Methods to avoid misunderstanding. Phosphosites were only considered if detected with high confidence (identification FDR<1%) and high localisation confidence (localisation probability >0.75) in at least one replicate. This criterion was chosen to retain biologically relevant, low-abundance phosphosites, which are more difficult to identify and are often stochastically sampled in phosphoproteomics datasets. For statistical analyses, missing values within a given condition were imputed with a well-established algorithm (MLE) only when at least one observed value was present in that condition. Notably, they were replaced by values in the neighborhood of the observed intensities, rather than by globally low, noise-like values.

We agree that more stringent exclusion rules, such as those used by Geoghegan et al. (2022), are appropriate in some contexts. However, there is no universally accepted standard for missingness thresholds in phosphoproteomics, and different strategies reflect trade-offs between sensitivity and stringency. In our discovery-oriented approach, we deliberately prioritized biological coverage while maintaining data quality. Our main conclusions are supported by coherent biological patterns, rather than by isolated phosphosite measurements.

(12) For the metabolomics analysis it looks like 2 amastigote samples were compared against 4 promastigote samples. Why not triplicates of each?

We thank the reviewer for noticing this point. It is an error in the figure file (Sup figure S1). Four biological replicates of splenic amastigotes were prepared (H130-1, H130-2, H133-1 and H133-2). Amastigotes from 2 biological replicates (H131-1 and H131-2) were seeded for differentiation into promastigotes in 4 flasks (2 per biological replicate) that were collected at passage 2. We have updated the figure file accordingly.

Minor comments:

Are prior studies referenced appropriately?

Yes

Are the text and figures clear and accurate?

The write up is clear, with the data presented coherently for each method. The analyses that link everything together are well discussed. The figures are mostly clear (see below) and are well described in the legends. There is good use of graphics to explain the experimental designs and sample names - although it is unclear if technical replicates are defined in these figures.

We thank the reviewer for these positive comments. We now included the information on replicates in the overview figure (Figure S1).

As I have understood it, the authors have calculated the "phosphostoichiometry" using the ratio of change in the phosphopeptide to the ratio of the change in total protein level changes. This is detailed in the supplemental method (see below). Whilst this has normalised the data, it has not resulted in an occupancy or stoichiometry measurement, which are measured between 0-1 (0% to 100%). The normalisation has probably been sufficient and useful for this analysis, but this section needs to be re-worded to be more precise about what the authors are doing and presenting. These concepts are nicely reviewed by Muneer, Chen & Chen 2025 (PMID: 39696887) who reference seminal papers on determination of phosphopeptide occupancy - and may be a good place to start. An alternative phrase should be used to describe the ratio of ratios calculated here, not phosphostoichiometry.

We thank the reviewer for this insightful comment and fully agree with the conceptual distinction raised. The reviewer is correct that the approach used in this study does not measure absolute phosphosite occupancy or stoichiometry, which would indeed require dedicated experimental strategies and would yield values bounded between 0 and 1 (0–100%). Instead, we calculated a normalized phosphorylation change, defined as the ratio of the change in phosphopeptide abundance relative to the change in the corresponding total protein abundance (a ratio-of-ratios approach – see doi :10.1007/978-1-0716-1967-4_12), and we tested whether this normalized phosphorylation change differed significantly from zero. This normalization approach is comparable to those previously published in the « Experimental Design and Statistical Analysis of the Proteome and the Phosphoproteome » section of the following paper (DOI: 10.1016/j.mcpro.2022.100428).

Our intention was to account for protein-level regulation and thereby better isolate changes in phosphorylation dynamics. While this normalization is informative and appropriate for the biological questions addressed here, we agree that the term “phosphostoichiometry” is imprecise and not correct in this context.

In response, we (i) replaced the term “phosphostoichiometry” throughout the manuscript with a more accurate description, such as “normalized phosphorylation level”, or “relative phosphorylation change normalized to protein abundance”, and (ii) revised the corresponding Methods and Results text to clearly state that absolute occupancy was not measured.

This rewording will improve conceptual accuracy without altering the validity or interpretation of the results.

From the authors methods describing the ratio comparison approach: "Another statistical test was performed in a second step: a contrasted t-test was performed to compare the variation in abundance of each modified peptide to the one of its parent unmodified protein using the limma R package {Ritchie, 2015; Smyth, 2005}. This second test allows determining whether the fold-change of a phosphorylated peptide between two conditions is significantly different from the one of its parent and unmodified protein (paragraph 3.9 in Giai Gianetto et al 2023). An adaptive Benjamini-Hochberg procedure was applied on the resulting pvalues thanks to the adjust.p function of R package cp4p {Giai Gianetto, 2016} using the Pounds et al {Pounds, 2006} method to control the False Discovery Rate level."

The references have been formatted.

Several aspects of the figures that contain STRING networks are quite useful, particularly the way colour around the circle of each node to denote different molecular functions/biological processes. However, some have descended into "hairball" plots that convey little useful information that would be equally conveyed in a table, for example. Added to this, the points on the figure are identified by gene IDs which, while clear and incontrovertible, are lacking human readability. I suggest that protein name could be included here too.

We thank the reviewer for this comment but for readability we opted to keep the figure as is. We now refer to Tables 8, 9, and 12 that allow the reader to link gene IDs to protein name and annotation (if available).

It is also not clear what STRING data is being plotted here, what are the edges indicating - physical interactions proven in Leishmania, or inferred interactions mapped on from other organisms? Perhaps as supplemental data provide the Cytoscape network files so readers can explore the networks themselves?

We thank the reviewer for this comment. While the STRING plugin in Cytoscape enables integrated network-based analyses, it represents protein–protein associations as a single edge per protein pair derived from the combined confidence score. Consequently, the specific contribution of individual evidence channels (e.g. experimental evidence, curated databases, coexpression, or text mining) cannot be disentangled within this framework. However, this representation was considered appropriate for the present study, which focused on global network topology and functional enrichment rather than on the interpretation of individual interaction types. The information on stringency has been added to the Methods section and the Figure legends (adding the information on confidence score cutoff).

We decided not to submit the Cytoscape files as they were generated with previous versions of Cytoscape and the STRING plugin. Based on the differential abundance data shown in the tables it will be very easy to recreate these networks with the new versions for any follow up study.

The title of columns in table S10 panel A are written in French, which will be ok for many people particularly those familiar with proteomics software outputs, but everything else is in English so perhaps those titles could be made consistent.

We apologize and have translated the text in English.

I would suggest that the authors provide a table that has all the gene IDs of the Ld1S2D strain and the orthologs for at least one other species that is in TriTrypDB. This would make it easy to interrogate the data and make it a more useful resource for the community who work on different strains and species of Leishmania. Although this data is available it is a supplemental material file in a previous paper (Bussotti et al PNAS 2021) and not easy to find.

We thank the reviewer for this very useful suggestion and have added this table (Table S13).

Figure 5b - from the legend it is not clear where the confidence values were derived in this analysis, although this is explained in the supplemental method. Perhaps the legend can be a bit clearer.

We have the following statement to the legend: ‘Confidence values were derived as described in Supplementary Methods’.

Can the authors discuss why lactacystin was used? While this is a commonly used proteasome inhibitor in mammalian cells there is concern that it can inhibit other proteases. At the concentrations (10 µM) the authors used there are off-target effects in Leishmania, certainly the inhibition of a carboxypeptidase (PMID: 35910377) and potentially cathepsins as is observed in other systems (PMID: 9175783). There is a specific inhibitor of the Leishmania proteasome LXE-408 (PMID: 32667203), which comes closer to fulfilling the SGC criteria (PMID: 26196764) for a chemical probe - why not use this. Does lactacystin inhibit a different aspect of proteasome activity compared to LXE-408?

We have add the following justification to the results section (see also response above to comment 3 for reviewer 2): We chose the highly specific and irreversible proteasome inhibitor lactacystin over the typanosomatid-specific, reversible drug candidate LXE408 as the latter’s potent cytotoxicity can confound direct effects on protein turnover with secondary consequences of cell death, limiting its utility for dissecting proteasome function in living parasites.

The application of lactacystin is changing the abundance of a multitude of proteins but no precision follow up is done to identify if those proteins are necessary and/or sufficient from driving/blocking differentiation. This could be tested using precision edited lines that are unable to be ubiquitinated? There is a lack of direct evidence that the proteins protected from degradation by lactacystin are ubiquitinated? Perhaps some of these could be tagged and IP'd then probed for ubiquitin signal. Di-Gly proteomics to reveal ubiquitinated proteins? These suggestions should be considered as OPTIONAL experiments in the relevant section above.

We very much appreciate these very interesting suggestions, which we will be considered for ongoing follow-up studies.

In the data availability RNA-seq section the text for the GEO link is : (https://www.ncbi.nlm.nih.gov/geo/query/acc.cgi?acc= GSE227637) but the embedded link takes me to (https://www.ncbi.nlm.nih.gov/geo/query/acc.cgi?acc=GSE165615) which is data for another, different study. Also, the link to the GEO site for the DNA seq isn't working and manual searches with the archive number (BioProject PRJNA1231373 ) does not appear to find anything. The IDs for the mass spec data PRIDE/ProteomeXchange don't seem to bring up available datasets: PXD035697 and PXD035698

The links have now been rectified and validated. For those data that are still under quarantine, here is the login information: To access the data:

DNAseq data: https://dataview.ncbi.nlm.nih.gov/object/PRJNA1231373?reviewer=6qt24dd7f475838rbqfn228d 0

RNAseq data: https://www.ebi.ac.uk/biostudies/ArrayExpress/studies/E-MTAB-16528?key=65367b55-d77f4c06-b4bd-bc10f2dc0b14

Proteomic data:  http://www.ebi.ac.uk/pride

Phosphoproteomic data: http://www.ebi.ac.uk/pride

Significance

Strengths:

(1) The molecular pathways that regulate Leishmania life-stage transitions are still poorly understood, with many approaches exploring single proteins/RNAs etc in a reductionist manner. This paper takes a systems-scale approach and does a good job of integrating the disparate -omics datasets to generate hypotheses of the intersections of regulatory proteins that are associated with life-cycle progression.

We thank the reviewer for this positive assessment of our work.

(2) The differentiation step studied is from amastigote to promastigote. I am not aware that this has been studied before using phosphoproteomics. The use of the hamster derived amastigotes is a major strength. While a difficult/less common model, the use of hamsters permits the extraction of parasites that are host adapted and represent "normal", host-adapted Leishmania ploidy, the promastigote experiments are performed at a low passage number. This is a strength or the work as it reduces the interference of the biological plasticity of Leishmania when it is cultured outside the host.

We thank the reviewer for the acknowledgment of our relevant hamster system, for which we face many challenges (financial, ethical, administrative as protocols need to be approved by the French government).

Limitations:

Potential lack of appropriate replication (see above).

See response to comment 1.

Lack of follow up/validation of a novel signalling interaction identified from the systems-wide approach. There is a lack of assessment of whether a single signalling cascade is driving the differentiation or these are all parallel, requisite pathways. The authors state the differentiation is not driven by a single master regulator, but I am not sure there is adequate evidence to rule this in or out.

See response to comment 2 above.

The study applies well established techniques without any particular technical stepchange. The application of large-scale multi-omics techniques and integrated comparisons of the different experimental workflows allow a synthesis of data that is a step forward from that existing in the previous Leishmania literature. It allows the generation of new hypotheses about specific regulatory pathways and crosstalk that potentially drive, or are at least active, during amastigote>promastigote differentiation.

We thank the reviewer for these positive comments.

This manuscript will have primary interest to those researchers studying the molecular and cell biology of Leishmania and other kinetoplastid parasites. The approaches used are quite standard (so not so interesting in terms of methods development etc.) and given the specific quirks of Leishmania biology it may not be that relevant to those working more broadly in parasites from different clades/phyla, or those working on opisthokont systems- yeast, humans etc. Other Leishmania focused groups will surely cherry-pick interesting hits from this dataset to advance their studies, so this dataset will form a valuable reference point for hypothesis generation.

We thank the reviewer for this assessment and agree that our data sets will be very valuable for us and other teams to generate hypotheses for follow-up studies.

Relevant expertise: Trypanosoma & Leishmania molecular & cell biology, RNA-seq, proteomics, transcriptional/epigenetic regulation, protein kinases - some experience of UPS system.

I have not provided comment on the metabolomics as it is outside my core expertise. However, I can see it was performed at one of the leading parasitology metabolomics labs.

We thank the reviewer for sharing expertise, investing time and intelligence in the assessment of our manuscript, and the highly constructive criticisms provided.

Reviewer #3 (Evidence, reproducibility and clarity):

Summary:

The study presents a comprehensive multi-omics investigation of Leishmania differentiation, combining genomic, transcriptomic, proteomic, phospho-proteomic and metabolomic data. The authors aim to uncover mechanisms of post-transcriptional and post-translational regulation that drive the stage-specific biology of L. donovani. The authors provide a detailed characterization of transcriptomic, proteomic, and phospho-proteomic changes between life stages, and dissect the relative contributions of mRNA abundance and protein degradation to stage-specific protein expression. Notably, the study is accompanied by comprehensive supplementary materials for each molecular layer and provides public access to both raw and processed data, enhancing transparency and reproducibility. While the data are rich and compelling, several mechanistic interpretations (e.g., "feedback loops," "recursive networks," "signaling cascades") are overstated. Similarly, the classification of gene sets as "regulons" is not adequately supported, as no common regulatory factor has been identified and only a single condition change (amastigote to promastigote) was assessed.

We thank the reviewer for these comments and have corrected the manuscript to eliminate all unjustified mechanistic interpretations.

Major Comments:

(1) Across several sections (incl abstract, L559-565, L589-599, L600-L603, L610-612, L613-614, L625, L643-645, L650-652), the manuscript describes "recursive or self-controlling networks", "signaling cascades", "self-regulating", and "recursive feedback loops" - involving protein kinases, phosphatases, and translational regulators. While the data convincingly demonstrate stage-specific changes in phosphorylation and abundance changes in key molecules, the language used implies causal, direct and directional regulatory relationships that have not been experimentally validated.

We agree with the reviewer and have corrected the text, replacing all expressions that may allude to causal or directional relationships by more neutral expressions such as ‘coexpression’.  

(2) Co-expression and shared function alone do not define a regulon (L363, and several other places in the manuscript). A regulon also requires the gene set to be regulated by the same factor, for which there is no evidence here. Regulons can be derived from transcriptomic experiments, but then they need to show the same transcriptional behavior across many biological conditions, while here just 1 condition change is evaluated. Therefore, this analysis is conventional GO enrichment analysis and should not be overinterpreted into regulons.

We agree with the reviewer and have replaced ‘regulon’ with ‘co-regulated gene clusters’ (or similar).

(3) LFQ intensity of 0 (e.g., L389): An LFQ intensity of 0 does not necessarily indicate that a protein is absent, but rather that it was not detected. This can occur for several reasons: (1) true biological absence in one condition, (2) low abundance below the detection threshold, or (3) stochastic missingness due to random dropout in mass spectrometry. While the authors state that adjusted p-values for the 1534 proteins exclusively detected in either amastigotes or promastigotes are below 0.01, I could not find corresponding p-values for these proteins in Table 8 ('Global_Proteomic'). An appropriate statistical method designed to handle this type of missingness should be used. In this context, I also find the following statement unclear: "identified over 4000 proteins at each stage in at least 3 out of 4 biological replicates, representing 3521 differentially expressed proteins (adjusted p-value < 0.01), 1534 of which were exclusively detected in either ama or pro." If a protein is exclusively detected in one stage, then by definition it should not be detected in that number of replicates at both stages. This apparent contradiction should be clarified.

We fully agree with the reviewer, an LFQ intensity of 0 may results from various reasons. We realize that our wording may have been ambiguous. For clarity, we have modified the original text to: ‘Label-free quantitative proteomic analysis of 4 replicates of amastigotes and derived promastigotes identified over 4000 proteins, including 1987 differentially expressed proteins (adjusted p-value < 0.01), and 1534 that were exclusively detected in either ama or pro (Figure 3A left panel, Table 6).’ We also modified the legend of the Figure 3B. Concerning missing values that could be either missing not at random (MNAR) or missing completely at random (MCAR), rather than introducing potentially misleading imputed values, we chose to treat these missing values as genuine stage-specific differences (presence/absence): quantitative statistics are restricted to proteins with measurable LFQ in both stages, while proteins with consistent presence in one stage and non-detection in the other are reported as stage-restricted detections. We believe this strategy is transparent and minimizes modeling assumptions, while still highlighting robust stage-specific signals. Our approach is supported by independent validation through RNA-seq data, which corroborates the differential presence/absence patterns observed at the protein level. Furthermore, our enrichment analyses reveal significant over-representation of specific biological terms among these stage-specific proteins, providing biological coherence to these findings. Therefore, we believe our conservative approach of treating these as genuine presence/absence differences, validated by orthogonal data, is more appropriate than introducing imputed values based on arbitrary statistical assumptions.  

(4) L412 - Figure 3B: The figure shows proteins with infinite fold changes, which result from division by zero due to LFQ intensity values of zero in one of the compared conditions. As previously noted, interpreting LFQ zero values as true absence of expression is problematic, since these zeros can arise from several technical reasons - such as proteins being just below the detection threshold or due to stochastic dropout during MS analysis. Therefore, the calculated fold changes for these proteins are likely highly overestimated. This concern is visually supported by the large gap on the y-axis (even in log scale) between these "infinite" fold changes and the rest of the data. Moreover, given Leishmania's model of constitutive gene expression, it seems biologically implausible that all these proteins would be completely absent in one stage. This issue applies not only to Figure 3B, but also to the analyses presented in Figures 4D and 4E.

We thank the reviewer for this comment. To clarify this section, we modified the text as follows: ‘Only expression changes were considered that either showed statistically significant differential abundance at both RNA and protein levels (p < 0.01), or showed significant RNA changes (p < 0.01) with the corresponding protein being detected in only one of the two stages. These latter proteins are identified by signals that were arbitrarily placed at the upper (detected in ama) or the lower (detected in pro) parts of the graph. Whether these proteins just escape detection due to low expression or are truly not expressed remains to be established.’ We also deleted the ‘infinity’ symbol from the Figure.

Minor Comments:

Methods

L132: Typo: "A according" should be "according."

The ‘A’ refers to RNase A. We added a comma for clarification (…RNase A, according to…)

L158: How exactly were somy levels calculated? Please specify the method used, as I could not find a clear description in the referenced manuscript.

We thank the reviewer for this comment. Aside the already quite detailed description in Methods and the reference there to the paper describing the pipeline, we now added a link to the description of the karyotype module of the giptools package (https://gip.readthedocs.io/en/latest/giptools/karyotype.html). There the following explanation can be found: “The karyotype module aims at comparing the chromosome sequencing coverage distributions of multiple samples. This module is useful when trying to detect chromosome ploidy differences in different isolates. For each sample the module loads the GIP files with the bin sequencing coverage (.covPerBin.gz files) and normalizes the meancoverage values by the median coverage of all bins. The bin scores are then converted to somy scores which are then used for producing plots and statistics.” The description then goes into further detail.  

L158: Chromosome 36 is not consistently disomic, as stated. It has been observed in other somy states (e.g., Negreira et al. 2023, EMBO Reports, Figure 1), even if such occurrences are rare in the studied context. Normalizing by chr36 remains a reasonable choice, but it would be helpful to confirm that the majority of chromosomes appear disomic post-normalization to support the assumption that chr36 is disomic in this dataset as well.

We thank the reviewer for this comment. Unlike the paper cited above (using longterm cultured promastigotes), our analysis uses promastigote parasites from early culture adaptation (p2) that were freshly derived from splenic amastigotes known to be disomic (and confirmed here), which represents an internal control validating our analysis.

L163: Suggestion: Cite the GIP pipeline here rather than delaying the reference until L173.

Corrected

L188: "Controlled" may be a miswording. Consider replacing with "confirmed" or "validated."

Corrected to ‘validated’

L214: Please specify which statistical test was used to assess differential expression at the protein level. L227: Similarly, clarify which statistical test was applied for determining differential expression in the phospho-proteomics data.

As noted in the Methods section, a limma t-test was applied to determine proteins/phosphoproteins with a significant difference in abundance while imposing a minimal fold change of 2 between the conditions to conclude that they are differentially abundant {Ritchie, 2015; Smyth, 2005}.

Results

L337-339: The interpretation here is too speculative. Phrases like "suggesting" and "likely" are too strong given the evidence presented. Alternative explanations, such as mosaic variation combined with early-stage selective pressure in the culture environment, should be considered.

We thank the reviewers for these suggestions and have reformulated into: ‘In the absence of convergent selection, it is impossible to distinguish if these gene CNVs provide some strain-specific advantage or are merely the result of random genetic drift.’

L340: The "undulating pattern" mentioned is somewhat subjective. To support this interpretation, consider adding a moving average (or similar) line to Figure 3A, which would more clearly highlight this trend across the data points.

These lines have been added to Figure 1C (not 3A).

L356: It may be more accurate to say "control of individual gene expression," since Leishmania does have promoters - the key distinction is that initiation does not occur on a gene-by-gene basis.

Corrected

L403-405: The statement "this is because these metabolites comprise a glycosomal succinate shunt..." should be rephrased as a hypothesis rather than a definitive explanation, as this causal link has not been experimentally validated.

Thank you for the comment – we followed your advice.

L407: Replace "confirming" with "matching" to avoid overstating the agreement with previous observations.

Corrected

L408: Replace "correlated" with "matched" for more accurate interpretation of results.

Corrected

L433: It is unclear how differential RNA modifications were detected. Please specify which biological material was used, the number of replicates per life stage, and how statistical evaluation of differential modifications was performed.

This figure has now been updated using our statistically robust RNA-seq analysis conducted for the revision. See comments above.

L436: This conclusion appears incomplete. While the manuscript mentions transcript-regulated proteins, it should also note that other proteins showed discordant mRNA/protein patterns. A more balanced conclusion would mention both the matching and non-matching subsets.

We thank the reviewer for this comment and have made the necessary adjustments to better balance this conclusion.

L441: The phrase "poor correlation" overgeneralizes and lacks nuance. Earlier sections of the manuscript describe hundreds of genes where mRNA and protein levels correlate well, suggesting that mRNA turnover plays a key regulatory role. Please rephrase this sentence to clarify that poor correlation applies only to a subset of the data.

This has been corrected to ‘The discrepancies we observed in a sub-set of genes between….’.

L454: The claim that "epitranscriptomic regulation and stage-adapted ribosomes are key processes" should be supported with references. If this builds on previously published work, please cite it accordingly.

Corrected

L457: Proteasomal degradation is a well-established mechanism in Leishmania. These findings are interesting but should be presented in the context of existing literature (e.g. Silva-Jardim et al.2014, [PMID: 15234661]) rather than as entirely novel.

Corrected

L459: The authors shoumd add a microscopy image of promastigotes treated with lactacystin. This would provide insight into whether treatment affects morphology, as is known in T. cruzi (see Dias et al., 2008). It would be particularly informative if Leishmania behaves differently.

We added this information to Figure S7.

L472 + L481: Table 9 shows several significant GO terms not discussed in the manuscript. Please clarify how the subset presented in the text was selected.

We added this information to the text (‘some of the most significantly enrichment terms included …’).

L482: The argument that a single master regulator can be excluded is unclear. Could the authors please elaborate on the reasoning or data supporting this conclusion?

This statement was too speculative and has been removed. Instead, we added ‘Thus, Leishmania differentiation correlates with the expression of complex signaling networks that are established in a stage-specific manner’.

L494: The term "unexpected" may not be appropriate here, as protein degradation is a wellestablished regulatory mechanism in trypanosomatids. Consider omitting this term to better reflect the field's current understanding.

We deleted the term as suggested and reformulated to ‘….our results confirm the important role of protein degradation….’.

L543: The term "feedback loop" should be used more cautiously. The current data are correlative, and no interventional experiments are provided to support a causal regulatory loop between proteasomal activity and protein kinases. As such, this remains a hypothesis rather than a confirmed mechanism.

We fully agree and have toned down the entire manuscript, referring to feedback loops only as a hypothesis and not as a fact emerging from our datasets, which set the stage for future functional analyses.

Discussion

L555: As noted in L494, reconsider using the word "unexpected."

Removed

L589: The data do not fully support the presence of stage-specific ribosomes. Rather, they suggest differential ribosomal function through changes in abundance and regulation. Please consider rephrasing.

We thank the reviewer for this comment and have follow the advice reformulating the sentence according to the suggestion.

L657-658: The discussion of post-transcriptional and post-translational regulation of gene dosage effects would benefit from citing additional literature beyond the authors' own work. E.g. the study by Cuypers et al. (PMID: 36149920) offers a relevant and comprehensive analysis covering 4 'omic layers.

We apologize for this omission and now describe and cite this publication in the Results section when concluding the results shown in Figure 1.

L659-664: The reference to deep learning for biomarker discovery appears speculative and loosely connected to the current findings. As no such methods were applied in the study, and the manuscript does not clarify what types of biomarkers are intended, this statement could be seen as aspirational rather than evidence-based. Consider either omitting or elaborating with clear justification.

We agree and have deleted this section.

L690 + L705 (Figure 2): The phrase "main GO terms" is vague. Please clarify the criteria for selecting the GO terms shown - were they chosen based on adjusted p-value, enrichment score, or another metric? Additionally, define "cluster efficiency," explaining how it was calculated and what it represents.

Corrected to ‘some of the most significantly enriched GO terms’.

Referee cross-commenting

Overall, I think the other reviewers' comments are fair. They seem to align particularly on the following points:

(1) Reviewers agree that this is a comprehensive body of work with original contributions to the field of Leishmania/trypanosomatid molecular biology, and that it will serve as a valuable reference for hypothesis generation.

(2) Several reviewers raise concerns about overinterpretation of the data, particularly regarding regulatory networks, regulons, and master regulators. The interpretation and large parts of the discussion are considered too speculative without additional functional validation.

(3) There are comments about the incorrect statistical treatment of missing values in the proteomics experiments, which affects confidence in some of the conclusions.

(4) While the correlation between the two RNA-Seq replicates is high, the decision to include only two biological replicates is seen as unfortunate and not ideal for statistical robustness.

(5) The use of lactacystin should be more clearly motivated, and its limitations discussed in the context of the experiments.

Even though I did not remark on the last two points (4 and 5) in my own review, I agree with them.

We thank the reviewer for this cross-comparison, which served us as guide to revise our manuscript. We believe that we have responded to all these concerns.

Reviewer #3 (Significance):

This study provides a rich, integrative multi-omics dataset that advances our understanding of stage-specific adaptation in the transcriptionally unique parasite Leishmania. By dissecting the relative contributions of mRNA abundance and protein turnover to final protein levels across life stages, the authors offer valuable insights into post-transcriptional and post-translational regulation. The work represents a resource-driven yet conceptually informative contribution to the field, with comprehensive supplementary materials and transparent data sharing standing out as additional strengths.  

However, the mechanistic insights proposed are speculative in several places and require more cautious language. The study is most impactful as a resource and descriptive atlas, initiating hypotheses for future validation. The broad scientific community working on Leishmania, trypanosomatids, and post-transcriptional regulation in eukaryotes would benefit from this work.

We thank the reviewer for this positive assessment and have modified the manuscript to further emphasize its strength as an important resource to incite mechanistic follow-up studies.

Field of reviewer expertise: multi-omics integration, bioinformatics, molecular parasitology, transcriptomics, proteomics, metabolomics, Leishmania, Trypanosoma.

Reviewer #4 (Evidence, reproducibility and clarity):

Summary:

This study investigates the regulatory mechanisms underlying stage differentiation in Leishmania donovani, a parasitic protist. Pesher et al., aim to address the central question of how these parasites establish and maintain distinct life cycle stages in mostly the absence of transcriptional control. The authors employed a five-layered systems-level analysis comparing hamster-derived amastigotes and their in vitro-derived promastigotes. From those parasites, they performed a genomic, transcriptomic, proteomic, metabolomic and phosphoproteomic analysis to reveal the changes the parasites undertook between the two life stages.

The main conclusion stated by the authors are:

- The stage differentiation in vitro is largely independent of major changes in gene dosage or karyotype.

- RNA-seq analysis identified substantial stage-specific differences in transcript abundance, forming distinct regulons with shared functional annotations. Amastigotes showed enrichment in transcripts related to amastins and ribosome biogenesis, while promastigotes exhibited enrichment in transcripts associated with ciliary cell motility, oxidative phosphorylation, and posttranscriptional regulation itself.

- Quantitative phosphoproteome analysis revealed a significant increase in global protein phosphorylation in promastigotes. Normalizing phosphorylation changes against protein abundance identified numerous stage-specific phosphoproteins and phosphosites, indicating that differential phosphorylation also plays a crucial role in establishing stage-specific biological networks. The study identified recursive feedback loops (where components of a pathway regulate themselves) in post-transcriptional regulation, protein translation (potentially involving stage-specific ribosomes), and protein kinase activity. Reciprocal feedback loops (where components of different pathways cross-regulate each other) were observed between kinases and phosphatases, kinases and the translation machinery, and crucially, between kinases and the proteasomal system, with proteasomal inhibition disrupting promastigote differentiation.

We thank the reviewer for the time and implication dedicated to our manuscript.  

Further details are organised by order of apparition in the text:

Material and Methods: while the authors are indicating some key parameters, providing the codes and scripts they used throughout the manuscript would improve reproducibility.

We thank the reviewer for this comment and added the URL for the codes to the data availability section.

Why only 2 biological replicates for RNA while the others layers have 3 or 4?

We agree with the other reviewers and have repeated this analysis to have statistically more robust results.

Is the slight but reproducible increase in median coverage observed for chr 1, 2, 3, 4, 6 and 20 stable on longer culture derived promastigotes and sandfly derived promastigotes ?

No, as published in Barja et al Nature EcolEvol 2017 (PMID: 29109466) and Bussotti et al PNAS 2023 (PMID: 36848551), these minor fluctuations are not predicting subsequent aneuploidies in long-term culture nor in sand fly-derived promastigotes. This information has been added to the text.

Is this change of ploidy a culture adaptation representation rather than a life cycle event as the authors discuss later on? (This is probably an optional request that would be nice to include, if the authors have performed the sequencing of such parasites. Otherwise, it should be mentioned in the discussion).

Yes, this is a well-known culture adaptation phenomenon, on which we have published extensively. We added this conclusion and the references to the text.

L333 "Likewise, stage differentiation was not associated with any major gene copy number variation (Figure 1C, Table 2)". The authors are looking here at steady differentiated stages rather than differentiation itself. "Likewise, stage differentiation was.." would be more appropriate.

We corrected this sentence to ‘Likewise, differentiation of promastigotes was not associated with any major gene copy number variation at early passage 2’.

L349-355: have the mRNA presenting change in abundance between stages been normalised by their relative DNA abundance ? Said otherwise, can the wave patterns observed at the genome level explain the respective mRNA level ? Can the authors plot in a similar way the enrichment scores in regards to the position on the genome and can the authors indicate if there is a positional enrichment in addition to the functional one they observe ? This may affect the conclusion in L356-358.

As noted above, we did not see any significant read depth changes at DNA level when comparing amastigotes and promastigotes. Thus there is no need to normalize the RNAseq results to DNA read depth. Furthermore, in our comparative transcriptomics analysis, we only consider 2-fold or higher changes in mRNA abundance (which is far beyond the non-significant read depth change we have observed on DNA level). Manual inspection of the enrichment scores with respect to position did not reveal any significant signal (other than revealing some overrepresented tandem gene arrays where all gene copies share the same location and GO term).

L415 "stage-specific expression changes correlate between protein and RNA levels, suggesting that the abundance of these proteins is mainly regulated by mRNA turn-over". Overstatement. Correlation does not suggest causation. "suggesting that the abundance of these proteins could be regulated by mRNA turn-over" would be more appropriate.

We thank the reviewer for this comment and have corrected the statement accordingly.

Figure 3B, could the authors clarify what are the "unique genes" that are on the infinite quadrants? It seems these proteins are identified in one stage and not the other. This implies that the corresponding missing values are missing non-at random (MNAR). Rather than removing those proteins containing NMAR from the differential expression analysis, the authors should probably impute those missing values. Methods of imputation of NMAR and MAR can be found in the literature. Indeed, the level of expression in one stage of those proteins is now missing, while it could strongly affect the conclusions the authors are drawing in figure 4E regarding the proteins targeted for degradation and rescued in presence of the proteasome inhibitor.

We thank the reviewer for this important comment. However, we would like to clarify several key points regarding the treatment of proteins identified in only one condition.

First, the reviewer assumes that proteins identified in one stage but not the other are necessarily missing not-at-random (MNAR). However, this cannot be definitively established, as these missing values could equally be missing completely at random (MCAR). Without additional information, categorizing them specifically as MNAR may be an oversimplification. More importantly, we have concerns about the reliability of imputation methods in this specific context. Algorithms designed to impute MNAR values (such as QRILC) replace absent data using random sampling from arbitrary probability distributions, typically assuming low intensity values. However, when no intensity value has been detected or quantified for a protein in a given condition, imputing an arbitrary low value raises significant concerns about data interpretation. Such imputed values would not reflect actual measurements but rather statistical assumptions that could introduce bias into downstream analyses. For instance, imputed values could lead to the conclusion that a protein is not differentially abundant, when in reality it is detected in one condition but completely absent in the other. In our view, there are two biologically plausible scenarios: either these proteins are expressed at levels below our detection threshold, or they are genuinely absent (or present at negligible levels) in the corresponding stage. Rather than introducing potentially misleading imputed values, we chose to treat these as genuine stage-specific differences (presence/absence), which results in infinite fold-changes in Figure 3B. Critically, our approach is strongly supported by independent validation through RNA-seq data, which corroborates the differential presence/absence patterns observed at the protein level. Furthermore, our enrichment analyses reveal significant over-representation of specific biological terms among these stagespecific proteins, providing biological coherence to these findings. These converging lines of evidence (proteomics, transcriptomics, and functional enrichment) strengthen our confidence that these represent biologically meaningful differences rather than technical artifacts.Therefore, we believe our conservative approach of treating these as genuine presence/absence differences, validated by orthogonal data, is more appropriate than introducing imputed values based on arbitrary statistical assumptions.To clarify this section, we modified the text as follows: ‘Only expression changes were considered that either showed statistically significant differential abundance at both RNA and protein levels (p < 0.01), or showed significant RNA changes (p < 0.01) with the corresponding protein being detected in only one of the two stages. These latter proteins are identified by signals that were arbitrarily placed at the upper (detected in ama) or the lower (detected in pro) parts of the graph. Whether these proteins just escape detection due to low expression or are truly not expressed remains to be established.’

L430-435 "These data fit with the GO [...] the ribosome translational activity (34)." This discussion feels out of place and context. It is too speculative and with little support by the data presented at this stage of the manuscript. It should be removed as Figure 3E or could be placed in the discussion and supplementary information.

We agree with the reviewer. In response to a comment from reviewer 1, we have moved both panels to Figure 2, which much better integrates these data.  

The authors present an elegant way to show stage specific degradation through the comparison of stage specific proteasome blockages that show rescue in ama of proteins present in pro and vice versa. L494 "reveal an unexpected but substantial" the term unexpected is inappropriate, as several studies have shown in kinetoplastids the essential role of protein turnover through degradation / autophagy during differentiation. Furthermore the conclusions may be strongly affected by the level of expression of the proteins in the infinite quadrants as we discussed above, and should be revised accordingly.

We rephrased the conclusion to ‘In conclusion, our results confirm the important role of protein degradation in regulating the L. donovani amastigote and promastigote proteomes and identify protein kinases as key targets of stage-specific proteasomal activities.’ Please see the response to comment 9 regarding the unique proteins.

L518 "These data reveal a surprising level of stage-specific phosphorylation in promastigotes, which may reflect their increased biosynthetic and proliferative activities compared to amastigotes." Overstatement. Could also be due to culture adaptation - What is the overlap of stage-specific phosphorylations with previous published datasets in other species of Leishmania? Looking at such comparisons could help to decipher the role of culture adaptation response, species specificity and true differentiation conserved mechanisms.

We agree with the reviewer and have toned this statement down by adding the statement ‘….or simply be a consequence of culture adaptation’.

The discussion is extremely speculative. While some speculation at this stage is acceptable, claiming direct link and feedback without further validation is probably far too stretched. For example, the changes of phosphorylation observed on particular sets of proteins, such as phosphatase and DUBs, need to be validated for their respective change of protein activity in the direction that fits the model of the authors. Those discussions should be toned down.

We agree with the reviewer and have strongly toned down the entire discussion, emphasizing the hypothesis-building character of our results, which provide a novel framework for future experimental analyses.

A couple of typos:

In the phosphoproteome analysis section, "...0,2 % DCA..." should be "...0.2 % DCA..." (use a decimal point).

L225 "...peptide match was disable." should be "...peptide match was disabled."

Both corrected

Reviewer #4 (Significance):

While there is not too much novelty around the emphasis of gene expression at post-translational level in kinetoplastid organisms, the scale of the work presented here, looking at 5 layers of potential regulations, is. Therefore, this study represents a substantial amount of work and provides interesting and comprehensive datasets useful for the parasitology community.

We thank the reviewer for this positive statement.

Several potential concerns regarding the biological meaning of the findings were identified. These include the limitations of in vitro systems promastigote differentiation potentially limiting the conclusions, the challenge of inferring causality from correlative "omics" data, and the complexities of functional interpretation of changes in phosphorylation and metabolite levels. The proposed feedback loops and functional roles of specific molecules would require further experimental validation to confirm their biological relevance in the natural life cycle of Leishmania, but that would probably fall out of the scope of this manuscript.

We agree with the reviewer and have modified pour manuscript throughout to remove any causal relationships. Indeed, this work is setting the stage for future investigations on dissecting some of the suggested regulatory mechanisms.

Area of expertise of the reviewers: Kinetoplastid, Differentiation, Signalling, Omics

Author response:

Public Reviews:

Reviewer #1:

Summary:

The authors aim to study mutational paths connecting WW domains with different binding specificities. Their approach combines an unsupervised sequence generative model based on RBMs with a path-sampling algorithm. The key result is that most intermediate sequences along the designed transition paths retain measurable binding activity in wet-lab assays, whereas paths containing the same mutations introduced in a randomized order are largely nonfunctional. This difference is attributed to epistatic interactions captured by the RBM model.

Strengths:

Exploring mutational paths in high-dimensional protein sequence space is a challenging problem. The computational framework used here is state-of-the-art and is strengthened by systematic experimental characterization of binding activity. The study is comprehensive in scope, including multiple transition paths both within and across WW specificity classes, and the integration of modeling with high-throughput experimental validation is a clear strength.

Weaknesses:

A major concern is whether the stated goal of specificity switching is fully achieved. Along the sampled transition paths, most intermediate variants appear to retain specificity close to either the initial or the final class, rather than exhibiting gradually shifting specificity. For example, in Figure 4G (Class I to Class II/III), binding appears largely binary, with intermediates behaving similarly to one of the endpoints. A similar pattern is observed in Figure 3H for the Class I to Class IV transition, where binding responses are close to 0 or 1. In this sense, the specificityswitching objective is only partially realized by assigning two endpoints with different specificity. This raises a broader conceptual question: is it possible that different WW specificities evolved from a common ancestor without passing through intermediates that exhibit mixed or intermediate specificity? If so, then inferring specificity-switching pathways purely from extant natural sequences may be fundamentally challenging.

This is a key question, which was one of the original motivations of our work. Both hypothesis of ‘abrupt switches’ (punctuated equilibria, corresponding to distinct specificities) and more gradual changes (smooth transition, through intermediate that exhibit mixed or intermediate specificity) are possible.

Many natural specificity-switching events have probably resulted from the need to adapt to environmental change and selection for a different specificity, which can be compatible with an abrupt change in specificity. Others may reflect the gradual evolution of promiscuous ancestral sequences to more specialized ones, loosing cross-reactivity. A molecular mechanism that could allow abrupt switching is gene duplication, a frequent mechanism for WW domain diversification, beyond standard mutational-driven evolution processes.  

As for the specificity-switching paths for WW domains found in this work, the presence of weakly responsive cross-reactive intermediates along the designed paths for I<->IV, and their absence in the I<->II path, suggests that designing promiscuous domains is hard (see also related response to point 3 of Reviewer 2) and generally not selected by natural evolution (as seen from the clear clustering of extant proteins in different specificity classes). 

For a small domain such as WW, mutations that favor some specificity classes are known to have detrimental effects on fundamental properties, such as folding kinetics and stability, see Ref [72]. It is possible that larger, less constrained protein domains could allow for more crossreactive variants and smoother specifity switching. However, experiments on fluorescent proteins looking for interpolation between two wave-lengths have shown that the switch was abrupt [Poelwijk et al. Nature Communications (2019)].

Our scope was to achieve a functional switch (imposed by the two extant end-points) through a path of designed, functional intermediates and to correctly predict, with our RBM model, the location of the specificity transition and of the cross-reactivity region (which we expected only along the I-IV path). This scope was successfully reached as demonstrated by experiments.  

Reviewer #2:

This is an extremely important work that shows how one can use generative models to construct specificity-switching mutational paths in complex fitness landscapes. The experimental evidence is very clear, and the theoretical tools are innovative.

The work will likely have a deep impact on future research aimed at understanding how evolution navigates fitness landscapes as well as reconstructing ancestral sequences.

The manuscript is extremely clear and well written, the experimental evidence is strong, and the methods are clearly described, so I do not have major issues to raise. A few minor issues are listed below.

(1) I consider the WW domain as an 'easy' case from the point of view of generative modelling. The domain is rather short, epistatic effects are not very strong (e.g. Boltzmann learning usually converges very quickly to a very paramagnetic state), and the resulting models are well interpretable (e.g. the hidden units of the RBM correlate well with subclasses).

This is not always (not often?) the case, however. In more complex proteins, the learning procedures can be slower and the resulting models less interpretable. Just for completeness, perhaps the authors could comment on the generality of the results and what they would expect for other systems based on their experience.

We agree with Reviewer 2 that WW sequences are short and simple to handle from a computational point of view, and was chosen for this reason to test the design of full mutational paths (after having benchmarked it to lattice-protein models, see Refs. [30] and [44]). Our work gives additional support to the effectiveness of generative models learned from sequence data.  This said, from a biological point of view, WW is a highly constrained domain, see comment by Reviewer 1 above and our answer.

In longer and more complex proteins, we expect it will be more difficult to disentangle specificityswitching latent units, see Fernandez-de-Cossio-Diaz et al., Physical Review X 2023 for a discussion and a possible computational approach to this issue. Notice that, while relating the latent units to specificity classes was convenient, it was not used to generate the paths themselves. Therefore, we believe that our method is quite robust and easily generalizable to applications to more complex and longer proteins. As an illustration, we have recently used it to sample viral trajectories (more precisely, variants of the Receptor Binding Domain of the SARSCoV-2 spike protein) capable of escaping antibody recognition, see Huot et al., PNAS 2026. In this recent work, we projected the paths onto the principal antigenic space, defined by the top two Principal Components of the viral variant binding affinities to 32 antibodies. In this representation, sampled paths displayed trends similar to natural paths, drawn from the sequences sampled during the pandemics. This finding supports the applicability and interpretation of our method for more complex proteins.

(2) In Section 3.3, the authors say that direct paths connecting Class I and Class IV behave similarly to indirect paths, despite having lower scores according to the RBM. How generic is this? Does it also happen for other classes? This might be an important point to address, as direct paths are easier to sample.

We think that this finding, true for paths connecting classes I and IV, is not general. In a previous paper we have benchmarked our path-designing approach on simple models of insilico lattice proteins and shown that indirect path led to gains in the overall fitness (computed according with the ground-truth model) [Mauri, Cocco, Monasson, Physical Review E 2023, fig. 9-12].

In general, we would expect that indirect paths could explore alternative mutations, important to compensate for transitory destabilizing mutations that could occur along the path. We speculate that these stabilizing mutations happen for non-direct paths at its extremity near class-I wildtype. A slightly decrease in binding response to peptide C1 for direct path is nevertheless observed (see Suppl Table 4), but our experimental detection, focused on binding response, is not tailored to directly detect a difference in stability. When approaching the class-IV anchoring point, we observe that paths interpolating between classes I and IV are very constrained and show limited diversity, going through a funnel in sequence space corresponding to the direct path. We agree with Reviewer 2 that a more exhaustive comparison with direct paths would be interesting, and will add a sentence in conclusion.

(3) The path shown in Figure 4 goes through a region of non-functionality around sequences 1819. It seems that the sample path is basically exploring the functional regions for Class I and Class II/III separately, trying to approach the other class, but then it can't really make the switch.

By contrast, the path going from Class I to Class IV seems able to perform the functional switch in a single step (20-21) without losing too much of the function.

Perhaps the authors could better comment on this? Is this a limitation of the sampling method, or a fundamental biological fact?

Class I to Class IV paths and Class I to Class II paths fundamentally differ because the binding pocket in Class I WW domains is different from the one of Class IV WWs, while Classes I and II/III share the same binding region. This important difference may explain why class I specificity can switch to class IV specificity (steps 20-21), without completely loosing affinity to the peptide of class I. To investigate if the two binding regions are really independent or not, we have tested some additional specific mutations along the I-IV mutational paths. In our attempts to engineer cross-reactivity, we have observed that it is important to substantially lower affinity to class I peptide to acquire class IV specificity, in agreement with previous studies [72]. Moreover, the I to IV path seems to go through a funnel-like part in the region with no natural sequences, with the same transition intermediates obtained in several designed paths. This indicates that the Class I to Class IV functional switch is more constrained than the Class I to II switch. Let us also emphasize that our assessment of class specificity is based on one peptide for each class. It would be interesting to test multiple WW-binding peptides with similar biochemical properties to acquire a more complete view of the specificities. 

(4) On page 12, it is stated that the temperature was chosen to 1/3 to maximize the score. This is important and should be mentioned earlier (I didn't notice it until that point).

Section 3.5 explains that RBM samples can be biased, by lowering the sampling temperature to 1/3 to obtain high-scores sequences, which are more likely to be functional as proven in [Russ et al., Science 2020]. We acknowledge (as also noted by Reviewer 1) that this section comes at the end of the manuscript, while differences in scores along the path are shown before, so the discussion of this important point is somewhat delayed. We will add a sentence earlier in Results to explain this point.  

(5) On page 13, it is stated that: "However, the scores of the ancestral sequences along the phylogenetic pathways assigned by the RBM are significantly lower than the ones of the RBMdesigned sequences. This result is expected as ASR reconstruction does not take into account epistasis, differently from RBM, and we expect ASR sequences to generally be of lesser quality."

I was very surprised by this result. My own experience with ASR shows that, on the contrary, sequences found by ASR (via maximum likelihood) tend to have high scores in the (R)BM, and tend to be more stable than extant sequences. I attribute this to the fact that ASR typically finds a "consensus" sequence that maximizes the contribution to the score coming from the fields (the profile), which is typically dominant over the epistatic signal, resulting in a bigger score. Maybe the authors did not use maximum likelihood in the ASR? Some clarification might be useful here.

We agree with Reviewer 2 that the consensus sequence is an atypical sequence for an independent model with a large RBM score. We will update Figure 5 of the manuscript to show that this is also happening in our case. 

We use Maximum Likelihood in ASR but our ASR path corresponds to all internal nodes of the reconstructed tree joining the two extant sequences, not only to the most ancestral node. Overall, the ancestral sequences along the ASR paths are different from the consensus sequence (mean identity of 76% and 60% respectively). The most ancestral nodes in the paths  are also different from the consensus having 81% (paths between type I and IV domains) or 54%(paths between type I and II/III domains) similarity, and an RBM score  of -21, or -58, respectively. We agree that some ASR internal-node sequence have a higher score than the natural wild-types (extant sequences). This is shown in Fig. 6: several points have larger RBM score than the two anchoring points at the extremities of the path, possibly due to the fact that natural sequences are not always the most stable ones. As discussed in conclusion, ASR nodes have moreover generally better scores than the sequences obtained by sampling an independent model. Phylogenetic reconstruction implicitly takes into account some degree of co-variation between sites in natural sequences, as shown by the success of the use of the phylogenetic distance of a mutated sequence to the wild-type for predicting the fitness effect of these mutations [Laine, Mol. Biol. Evol. 2019]. 

To better show this effect we will update Figure 6, reporting also the scores of the « scrambled » sequences, which do not respect potential epistasis extracted by the RBM. It appears that ASR sequences generally have better scores than the scrambled sequences, and lower than RBM sequences (sampled at T=1/3). RBM models takes into account multiple-residues correlations, which could contribute to reaching better scores than ASR and BM models. Ongoing studies on larger proteins show that the score of sequences sampled from ASR reconstruction, including the Maximum Likelihood one, can still be improved according to the RBM score by a few mutations consistent with the ASR posterior probabilities (unpublished). 

Mistakes in the reference list will be amended in the updated version.

Note: This response was posted by the corresponding author to Review Commons. The content has not been altered except for formatting.

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Reply to the reviewers

1. General Statements [optional]

We thank to all reviewers on their careful consideration of our manuscript. We highly appreciate their thoughtful comments and suggestions, that helped us to improve the quality of our work. We address each comment point-by-point below.

2. Description of the planned revisions

__Reviewer #1 __

Minor comments:

Figure 5 would be more informative if it included more higher magnification images that would reveal the staining at the cellular level.

To fulfil the suggestion, we will perform a new round of immunostaining followed by high-resolution confocal imaging. This requires additional time for laboratory work.

__Reviewer #2: __

Major comments

1d. The authors tried to attribute the minor phenotype to the incomplete depletion of S100A4+ cells. However, it is possible that if the S100A4+ cells only represented a minor population, their function may be compensated by other populations. This might be confirmed by quantification of S100A4+ cells or S100A4-Cre; GFP+ cells in fibroblast or CD45 populations from images showed in Figure 5.

We will address this comment by performing required quantifications.

Moreover, we have now included data on the presence of S100A4+ cells in S100a4-Cre;DTA mice (Figure for Reviewers 5a,b; Supplementary Figure 7a,b in the revised manuscript), which demonstrate incomplete depletion of the S100A4+ cells in the nipple and the mammary gland. This is likely due to ongoing tissue remodeling and continuous S100A4+ replenishment/ supply. Another study using the same S100a4-Cre;DTA mouse model reported an efficient S100A4+ cell depletion in mandibular condyle (Tuwatnawanit et al., 2025), which suggests that the presence of S100A4+ cells in the S100a4-Cre;DTA mammary gland and nipple is due to tissue-specific dynamics rather than lack of depletion efficiency.

        We have included in Discussion: “Notably, we observed incomplete depletion of S100A4+ cells in the mammary gland and nipple. Interestingly, a study using the same S100a4-Cre;DTA mouse model reported complete S100A4+ cell depletion in the superficial layer of mandibular condyle46. This suggests that incomplete depletion of S100A4+ cells in nipple and mammary gland is due to tissue-specific dynamics, rather than lack of depletion efficiency, indicating a compensatory mechanism that can balance the cell loss.”

The images in Figure 5 and Figure S4 are difficult to confirm colocalization. A higher magnification image would be required for each panel. Furthermore, a precise quantification based on the current images would be more supportive of the conclusion regarding the discrepancy of the composition of S100A4 lineage between epidermis and mammary gland (lines 163-165).

To address this comment, we will perform a new round of immunostaining and high-resolution confocal imaging and quantifications and include the results in the fully revised manuscript.

Line 163, the author hypothesis the Langerhans cells due to morphology. Those cells should be able to be confirmed by a co-staining with F4/80 in addition to the current form of Fig 5h.

To address this comment, we will perform co-staining of GFP and F4/80 (or, eventually, AIF1, depending on antibody availability) and include the results in the fully revised manuscript.

Reviewer #3

Minor comments

Figure 2c: The H&E images are not fully convincing. Immunofluorescence analysis of epithelial architecture would support the authors' interpretation and should be feasible if tissues are already available.

We will perform immunostaining for epithelial markers, such as keratins, and include the results in the fully revised manuscript.

Figure 4f: The proliferation data are compelling, but the authors could extend this by examining how cell differentiation and epithelial organisation are affected.

We will perform immunostaining for epithelial markers (keratins, αSMA) and include the results in the fully revised manuscript.

Figure 5b: To more convincingly show that GFP+ cells contact endothelial cells, co-labelling with an endothelial marker such as CD31 would be helpful.

We will perform the requested co-labeling of GFP and CD31 and include the results in the fully revised manuscript.

Figure 5f-h: The structures referenced in the text (lines 159-163) should be clearly indicated on the immunofluorescence images.

We will incorporate these explanations into the new, high-resolution/detailed Figure 5 in the fully revised manuscript.

3. Description of the revisions that have already been incorporated in the transferred manuscript

Reviewer #1:

Major comments

1. It is rather difficult to conclude whether the observed nipple phenotype reflects an early embryonic/prepubertal defect in establishing the nipple stroma, is caused by a constitutive response to ongoing cell death, or a response to continuous DTA expression (or a combination of some of these).

The data raise a couple of additional questions: Is there a nipple phenotype at 3 wk of age? It would not be totally unsurprising if ablation of a major fraction of dermal fibroblasts in the nipple area would lead to an early embryonic/prepubertal phenotype but there is no data on this. Hence, is there a "congenital" nipple deformity, as concluded by the authors (line 191)?

We appreciate the reviewer’s insightful comments. We have now included data on embryonic nipple development. These data demonstrate abundant S100A4-lineage cells in E15.5 and E18.5 skin of S100a4-Cre;mT/mG embryos (Figure for Reviewers 1a, corresponding to Figure S3a in the revised manuscript) and normal appearance of nipple sheath in S100a4-Cre;DTA embryos at E18.5 (Figure for Reviewers 1b, corresponding to Figure S3b in the revised manuscript), suggesting no embryonic defect.

Unfortunately, we cannot provide data on 3-weeks old mice (we have not collected this timepoint previously and currently we do not have this mouse line alive). Instead, however, we provide in situ pictures of DTA and S100a4-Cre;DTA nipples at 7 weeks of age (Figure for Reviewers 1c; Figure S3c in the revised manuscript), which demonstrate that the phenotype of defective nipple is fully established at this timepoint. Because the late embryonic data did not support the “congenital” establishment of the nipple deformity and we could not provide any more data from early postnatal development, we have corrected the statement “we describe a congenital nipple deformity” in the discussion to “we describe a nipple deformity”.

Are there S100a4+ cells in the nipple area of pubertal S100a4-Cre/DTA mice? I.e. is there a continuous supply of new S100a4+ cells and thereby continuous cell death and DTA expression as one might expect based on the RNA-seq data?

The S100A4+ cells are present in the nipple area of S100a4-Cre;DTA mice, suggesting a continuous supply of new S100A4+ cells (Figure for Reviewers 1b, corresponding to Figure S3b in the revised manuscript; and Figure for Reviewers 5a,b, corresponding to Figure S7a,b in the revised manuscript). In the revised manuscript, we comment on this in Discussion: “Notably, we observed incomplete depletion of S100A4+ cells in the mammary gland and nipple. Interestingly, a study using the same S100a4-Cre;DTA mouse model reported complete S100A4+ cell depletion in the superficial layer of mandibular condyle46. This suggests that incomplete depletion of S100A4+ cells in nipple and mammary gland is due to tissue-specific dynamics, rather than lack of depletion efficiency, indicating a compensatory mechanism that can balance the cell loss.”

Figure for Reviewers 1 (Figure S3 in the revised manuscript): Embryonic and pubertal nipple phenotype. (a) Representative images of cleared whole-mount S100a4-Cre;mT/mG nipple tissue at embryonic developmental time-points: E15.5 and E18.5. Scale bar = 100 µm. (b) Immunofluorescent labeling for S100A4 on embryonic DTA and S100a4-Cre;DTA whole-mount skin (E18.5). Scale bar = 100 µm. (c) Representative in situ photographs of nipples from DTA and S100a4-Cre;DTA pubertal (7-weeks old) mice. Scale bar = 1 mm.

The subtitle on line 54 implies that that S100a4-Cre/DTA mice display a branching phenotype. However, it looks to me as if there is a pubertal outgrowth defect (as is also written in the body text, line 64) rather than a branching phenotype, potentially reflecting the much smaller size of S100a4-Cre/DTA mice (Fig. 2a). Unless there is a change in branch point frequency, I suggest rephrasing the title and discussion. Instead, I suggest the authors discuss the observed outgrowth delay considering the gross overall growth defect (Fig. 2a). If ductal outgrowth was normalized to the overall growth defect, would one still observe 'a delay in branching morphogenesis'?

We apologize for the section title confusion. We have analyzed branching frequency in 7-weeks-old females and observed reduced total number of branching points in S100a4-Cre;DTA mice (Figure for Reviewers 2a, corresponding to Figure 2f in the revised manuscript). A significant difference in number of branching points remained also after their normalization to body weight, (Figure for Reviewers 2c, corresponding to Figure 2h in the revised manuscript). We have now added the new quantifications to the revised manuscript with accompanying descriptions in the main text “Analysis of mammary epithelial development using whole-mount carmine staining revealed no significant differences in the prenatal establishment of the mammary epithelial tree but did reveal significantly delayed epithelial outgrowth and reduced branching in pubertal (7 weeks old) S100a4-Cre;DTA mice (Figure 2e,f). Normalization of epithelial outgrowth and branching to body weight indicates that the observed defect represents a mammary-specific impairment rather than a consequence of reduced body growth (Figure 2g,h).”.

__Figure for Reviewers 2 (Figure 2 in the revised manuscript): __Pubertal branching morphogenesis is delayed in S100a4-Cre;DTA. (a-c) The plots show total number of branching points (a), epithelial outgrowth [mm] normalized to body weight [g] (b), and total number of the branching points normalized to body weight [g] (c) in 7 weeks old DTA and S100a4-Cre;DTA mice. All plots show the mean ± SD, *p

Fig. 4e shows Masson's Trichrome and Picrosirius Red staining and the authors report the findings as follows (lines 120-124): "collagen fibers were loosened in the DTA nipples and more densely packed in the S100a4-Cre;DTA nipples". Perhaps the authors could help non-specialists to observe the loosened fibers and if they wish to make quantitative statements ("more densely packed"), such statements should be backed-up by quantifications.

Picrosirius Red staining viewed under polarized light is a classic way to assess collagen organization, thickness, and packing. Red / orange / yellow color typically marks thicker, more mature, and more tightly packed collagen fibers (often associated with type I collagen), while green color usually marks thinner, less organized, or less densely packed fibers (often associated with type III collagen or immature collagen). We had included this explanation in the Figure legend of the submitted manuscript already: “Typically, thicker collagen fibers exhibit stronger birefringence and appear red or orange, while thinner fibers exhibit weaker birefringence and appear green or yellow.” To help with the quantification, we have extracted the red channel and quantified color intensity. The results are shown in Figure for Reviewers 3, corresponding to Figure S4 in the revised manuscript. Moreover, we will also quantify the differences in pattern of the collagen fibers. The fibers in DTA nipples look shorter and more curved, while the fibers in S100a4-Cre;DTA nipples look longer and straighter, more aligned. The results will be included in the fully revised manuscript.

Figure for Reviewers 3 (Figure S4 in the revised manuscript): Collagen fibers are densely packed in S100a4-Cre;DTA nipples contain more . (a) Representative pictures of histological sections of DTA and S100a4-Cre;DTA stained for collagen by Picrosirius red. Polarized light images and the red channel (mature/densely packed collagen) are shown alongside detail pictures of selected regions A and B. Scale bar = 200 µm and 100 µm (in detail pictures). (b) Quantification of Intensity Mean Value for the red channel (densely packed collagen), showing statistically non-significant difference. The plot shows the mean ± SD, ns p > 0.05 (Mann-Whitney test), n = 3 DTA / 4 S100a4-Cre;DTA.

I found the Discussion on the various mouse models somewhat problematic. Overall, the paper is written is a way that it often remains unclear whether it refers to studies addressing the role of S100a4 itself, studies addressing the function of S100a4+ cells via ablation approaches (S100a4-Cre or S10 0a4-CreERT2 crossed with floxed DTA), or those where S100a4-Cre has been used to delete gene X/Y/Z. These are all very different experimental approaches where one approach is not necessarily informative when trying to understand the results from another one. The authors should make these points clear and consider whether all their discussion points are relevant.

We apologize for the confusion. We have carefully reviewed the references and their interpretations, and corrected them as necessary.

The abstract states S100a4 (fibroblast-specific protein 1) is "expressed by mesenchymal cells and has been implicated in the development of eccrine glands, hair follicles, and mammary branching morphogenesis". However, the study on eccrine glands (ref. 19) shows that S100A4+ cells play a role in eccrine gland development but it does not address the role of S100a4 itself, while the study on hair follicles (ref.20) in turn reports the expression pattern of S100a4 in hair follicles but does not address its function, nor the role of S100a4+ cells. Finally, I failed to find references in the paper to studies addressing the role of S100a4, or S100a4+ cells in the mammary gland.

Instead, the paper had references to studies where S100A4-Cre had been used to delete different genes and these mice had various mammary phenotypes - which, as indicated above, is a very different approach compared to deleting S100a4 or ablating S100a4+ cells.

Thank you for your comment. We addressed the concern in the Abstract and further in the Discussion. We revisited the present the cited studies more carefully, clearly distinguishing the different approaches and particular findings.

In our literature review, we also considered studies that used S100a4-Cre mouse model, to manipulate gene expression within S100A4+ cells. We believe that these studies bring indirect evidence of S100A4+ cell involvement in development and/or homeostasis of a tissue, such as mammary gland. Please, find the rephrased part of Abstract in the text, and below:

“S100A4 (S100 calcium binding protein A4, also known as fibroblast-specific protein 1) is expressed by mesenchymal cells and has been associated with hair follicle regeneration. S100A4-expressing cells have been implicated in the development of eccrine glands, and studies using S100a4-Cre to manipulate gene function have suggested that S100A4-expressing cells may contribute to mammary branching morphogenesis.”

__In Discussion (lines 197-200), __the authors write: "We described significant delay in mammary branching morphogenesis in puberty, confirming an important role for S100A4+ cells in mammary development, as it was previously described (refs 37-39)."

It should be noted that none of these studies addressed the role of S100A4+ cells:

• Ref 37 used S100a4-Cre to delete sharpin

• Ref 38 used the same Cre line to delete Ptch1, did not address the role of S100a4 or S100a4 expressing cells

• Likewise ref 39 deleted another gene using S100a4-Cre

Later on in Discussion, the authors compare the reported phenotype to previous studies (lines 248-255): "...targeting S100A4+ cells through knockout experiments can result in severe phenotypes, such as a reduction in adipose tissue (ref 26), skin phenotypes, a disrupted estrous cycle, reduced fertility (ref. 38), and complete infertility, hypogonadism and defects in pituitary endocrine function (ref. 28).

Of these, Ref. 26 used the same approach as the current study (S100a4-Cre; DTA) (Fig. 7A in the paper)

• these mice were significantly lean, with markedly reduced fat compared with the control mice - also the mice in the current study are very small, so perhaps they could also be described as 'lean'. Yet ref. 26 reports that female mice had comparable food uptake, respiratory exchange ratio and physical activity, and slightly increased energy expenditure

Ref. 38 (as mentioned above) reports deletion of Ptch1 using S100a4-Cre lines and these mice "displayed a disrupted estrous cycle and dramatically reduced fertility over 6.5 weeks". However, this has nothing to do with the approaches where Fsp1/S100a4+ cells are depleted with DTA. Likewise, reference 28 analyzed the phenotype of S00a4-Cre;Ptch1fl/fl mice. Obviously, deleting Ptch1 using S100a4-Cre mice is quite a different approach than "targeting S100A4+ cells" through knockout experiments". Ptch1 deletion leads to a combination of gain-of-function (of Hedgehog activation) and loss-of-function (loss of Hh-independent functions of Ptch1) and hence comparisons with these phenotypes is rather challenging. I suggest the authors focus their phenotype comparisons to ref. 26 where S100a4/Fsp1+ cells were ablated with DTA, i.e. the same approach as in the current study.

Please, find the rephrased part of Discussion in the text (lines 236-256), and below:

“A key consideration when interpreting studies involving S100A4 is that fundamentally different experimental approaches have been used to investigate its role. These include descriptive analyses of S100A4 expression, functional studies targeting the S100A4 protein itself, genetic models using S100a4-Cre to manipulate unrelated genes in S100A4-expressing cells, and ablation models such as S100a4-Cre;DTA, which deplete S100A4⁺ cells. These approaches are not equivalent and provide distinct types of information. In the present study, we specifically assess the consequences of ablating S100A4-expressing cells, and comparisons to other studies should therefore be interpreted within this context.

Studies using S100a4-Cre to manipulate specific signaling pathways (e.g. Wnt or Hedgehog signaling via gene deletion) in S100A4-expressing cells have reported diverse phenotypes, including effects on fertility and endocrine function28,34. However, these phenotypes primarily reflect the consequences of pathway perturbations within S100A4-expressing cells rather than the role of S100A4⁺ cells themselves. This is fundamentally different from the ablation approach used here, which removes the S100A4⁺ cell population.

In contrast, studies employing S100a4-Cre–driven DTA–mediated ablation represent a directly comparable approach. Such studies have reported systemic phenotypes, including reduced adipose tissue and altered metabolic parameters26, indicating that S100A4-expressing cells contribute to multiple aspects of tissue homeostasis. Consistent with these previous reports, S100a4-Cre;DTA mice used in our study were significantly smaller than their littermates. Our findings extend these observations by identifying a specific and previously unrecognized role for this cell population in nipple morphogenesis.”

I find the Discussion is somewhat off the topic by starting with WHO recommendations on breastfeeding and linking this to observed mouse phenotype. Overall, the discussion is rather long and from time-to-time more like a literature review. I would recommend keeping the Discussion more succinct and focused.

To improve the conciseness and focus of Discussion, we have deleted this part of text.

**Referee cross-comenting**

I agree with the comments of other reviewers. However, to me it seems that the analysis of S100a4 knockout mice would not be feasible within a reasonable timeframe and would represent a study of its own. My understanding was that the authors were not interested in S100a4 itself. Rather, S100a4-Cre was used as a tool to understand the importance of a certain (fibroblast) cell population for mammary gland morphogenesis.

Indeed, our goal was to study the role of a specific cell population (S100A4+ cells) in mammary gland morphogenesis, not to study the role of S100A4 protein per se.

Reviewer #1 (Significance (Required)): General assessment:

This study reveals the importance of the S100a4+ cell lineage for nipple formation while showing the same cells are dispensable for mammary gland morphogenesis. The main limitation is that it remains unclear whether the observed nipple phenotype is derived from an early embryonic/prepubertal defect in establishing the nipple stroma, is caused by a constitutive response to ongoing cell death, or a response to continuous DTA expression (or a combination of some of these). Hence its relevance as a model of human inverted nipple condition remains rather speculative.

Thank you for consideration of our work and valuable feedback. We did not intend to claim that S100a4-Cre;DTA mouse represents a model of human inverted nipple condition. However, considering morphological features, it might resemble it. We now rephrased the Discussion so it is clearer and more concise.

Reviewer #2

Major comments:

1. My key concern is the discussion part. I think the authors need to re-organize/re-phrase the discussion part, it confused me a bit in terms of logic, phrases and interpretation of literatures.

We have significantly re-organized and re-phrased the Discussion.

Here are few examples:

1. The lines 195-199 contain lot of repeated information

We have rephrased the paragraph and removed repeated information. The new text can be found in lines 201-206 in the revised manuscript.

1. The authors mentioned the studies in ref 26,28 and 38 using "targeting S100A4+ cells through knockout experiment can result in sever phenotypes". This is very misleading. Those studies using the same (or similar if the origin is different) S100A4-Cre line as the current study but induced the activation of Wnt and sHH signalling pathways, respectively. The observed phenotypes are largely due to the pathway function, rather than the S100A4 gene or normal S100A4+ cell itself. This is significantly differed from the current study.

We apologize for the confusion; we have now rephrased our claims (lines 236-256):

“A key consideration when interpreting studies involving S100A4 is that fundamentally different experimental approaches have been used to investigate its role. These include descriptive analyses of S100A4 expression, functional studies targeting the S100A4 protein itself, genetic models using S100a4-Cre to manipulate unrelated genes in S100A4-expressing cells, and ablation models such as S100a4-Cre;DTA, which deplete S100A4⁺ cells. These approaches are not equivalent and provide distinct types of information. In the present study, we specifically assess the consequences of ablating S100A4-expressing cells, and comparisons to other studies should therefore be interpreted within this context.

Studies using S100a4-Cre to manipulate specific signaling pathways (e.g. Wnt or Hedgehog signaling via gene deletion) in S100A4-expressing cells have reported diverse phenotypes, including effects on fertility and endocrine function28,34. However, these phenotypes primarily reflect the consequences of pathway perturbations within S100A4-expressing cells rather than the role of S100A4⁺ cells themselves. This is fundamentally different from the ablation approach used here, which removes the S100A4⁺ cell population.

In contrast, studies employing S100a4-Cre–driven DTA–mediated ablation represent a directly comparable approach. Such studies have reported systemic phenotypes, including reduced adipose tissue and altered metabolic parameters26, indicating that S100A4-expressing cells contribute to multiple aspects of tissue homeostasis. Consistent with these previous reports, S100a4-Cre;DTA mice used in our study were significantly smaller than their littermates. Our findings extend these observations by identifying a specific and previously unrecognized role for this cell population in nipple morphogenesis.”

1. In the lines 253-255, why the author believe complete S100A4+ depletion would leads to the fatal of mouse? Is there study suggest that? Or have authors checked the expression of S100A4 in the S100A4-Cre;DTA model to confirm the efficiency?

We have now included, also in response to other Reviewers’ comments, data on S100A4 expression in the S100A4-Cre;DTA model (Figure for Reviewers 5, corresponding to Figure S7 in the revised manuscript), and commented on these results in lines 257-262: “Notably, we observed incomplete depletion of S100A4+ cells in the mammary gland and nipple. Interestingly, a study using the same S100a4-Cre;DTA mouse model reported complete S100A4+ cell depletion in the superficial layer of mandibular condyle48. This suggests that incomplete depletion of S100A4+ cells in nipple and mammary gland is due to tissue-specific dynamics, rather than lack of depletion efficiency, indicating a compensatory mechanism that can balance the cell loss.”

In Fig. 1, the authors described the impaired nursing capacity of S100A4-Cre;DTA dam. However, it seems the little size is also smaller (Fig 1a). Do authors have any explanation or hypothesis?

Thank you for this insightful observation. It is well established that metabolic and nutritional condition directly affect female reproductive functions. Adult S100A4-Cre;DTA mice are generally smaller compared to their litter counterparts, potentially because of lower body fat content or other anatomic/metabolic condition that might negatively influence fecundity, for instance, lowering ovulation rate and/or embryonic survival. In support of this, earlier studies have reported a positive correlation between growth rate/body condition and litter size (Eisen & Durrant, 1980). Unfortunately, in the case of S100A4-Cre;DTA mice, we can only speculate about the possible explanations, as we do not have supporting data which could confirm it.

In lines 181-184, the authors states "the results showed that the tissue reacted to a foreign chemical or an endogenous compound....." , which results are referring here? I could not find any inflammation related GO terms in figure 6b. It would be more accurate to specify them in lines 179-181, which appears to be a technical statement rather than a result in current form.

Thank you for this comment. Indeed, there are no GO terms explicitly labeled as “inflammation” and “repair”; however, several GO terms are functionally related to these processes. Our interpretation was based on broader biological context rather the explicit annotation. To clarify this, we revisited the text and included GO terms that reflect the tissue response (lines 187-193).

“The GO terms indicated that the tissue reacted to a foreign chemical or an endogenous compound (xenobiotic metabolic process, cellular response to xenobiotic stimulus, response to xenobiotic stimulus, epoxygenase P450 pathway), and responded to inflammation and repair (actin filament-based process, actin cytoskeleton organization; eicosanoid and lipid metabolic processes) (Figure 6b).”

The lines 182-184 was not clear. Does the author refer the "nipple tissue response" in general as malfunction of development or inflammation and tissue repair as mentioned in the previous sentence? If the later cases, the authors should consider the failure of lactation might mimic the involution, which may cause the apoptosis and inflammation as well. This might be independent of the DTA expression.

Thank you for raising this point. Indeed, in this line, we refer to ongoing tissue inflammation and repair. We also considered the hypothesis that the ejection incapability (and consecutive milk stasis) triggers involution. However, tissues were collected within a few hours after parturition, when only very early signs of involution, if any, would be detectable; therefore, we expect minimal influence of involution. To reflect this comment, we added new text to the Discussion (lines 272– 277). “The observed tissue response can be also associated with hallmarks of mammary involution, the process which is triggered by the milk stasis. However, the tissues were collected within few hours after parturition, when the effect of involution should be minimal53. Rather, we hypothesize that immune cell recruitment, and the upregulation of the lipid skin barrier might be caused in response to the continuous apoptosis of S100A4+ cells and their replacement.”

Minor comments:

1. The authors demonstrated in Figure S1 and lines 92-96 that no significant differences were observed in pituitary glands and ovaries in S100a4-Cre:DTA and DTA mice. Have the authors checked the S100A4 expression or lineage cells in these organs, or have been reported by others?

Yes, we checked the S100A4-lineage cells in the pituitary gland and ovary and have now included the results here (Figure for Reviewer 4a,b corresponding to Figure S1a,b in the revised manuscript), along with relevant text description (lines 94-95 in the revised manuscript). “We observed S100A4-lineage traced cells in pituitary gland and ovaries using S100a4-Cre;mT/mG model (Figure S1a,b).” The presence of S100A4+ cells in these organs was also reported previously (Ren et al., 2019).

Figure for Reviewers 4 (Figure S1 in the revised manuscript): S100A4-lineage cells are abundant in the pituitary gland and ovary. (a) Representative images of a cleared whole-mount pituitary gland from a S100a4-Cre;mT/mG mouse. (b) Representative images of a cleared whole-mount ovary from a S100a4-Cre;mT/mG mouse. Scale bar = 100 µm.

The authors have performed live imaging to evaluate the contraction of alveoli. It would be better to include a video together with the snapshots showed in Figure S2.

We have included the videos as supplementary movies, Movie S1 (DTA) and Movie S2 (S100a-Cre;DTA).

Since the study is mainly using S100a4, it would be better to avoid using FSP1 in the results, for example Fig 5h.

We apologize for this oversight; it has now been corrected.

What does L1 stand for? Lactation Day 1? It should be spelt out in the first instance.

Yes, indeed, L1 is lactation day 1. Please note that it was already spelled out in the first version of the manuscript, now in line 48.

Line 150. Figure S4 should be Figure S4a.

(Please note, that by adding new Supplementary figures, this comment is referring to Figure S6 in the new version of manuscript.) Thank you for this comment. In the text, we state “GFP+ cells were spread throughout the fat pad but were also localized in the periepithelial stroma and infiltrated the epithelium”. This we show in Figure S6a and in S6b; therefore, we now changed the reference accordingly, as it might be more accurate.

**Referee cross-comenting**

I agree with the other reviewers, as well as the Consultation Comments. The manuscript would benefit greatly from a thoroughly optimised Discussion section to address issues raised by all reviewers.

__ Reviewer #2__ (Significance (Required)):

• Overall, this study is well designed and the key findings are valid, especially the role of S100A4 during nipple development is novel and interesting.

-One limitation of the study is that RNA-seq was performed using a mixture of all cell types present in the nipple. While this approach is reasonable-given that depletion of the S100A4+ lineage may exert both direct and indirect effects contributing to nipple dysfunction-it should be more clearly acknowledged and discussed in the manuscript. Additionally, this experimental design may limit the utility of the dataset for other researchers interested in nipple development and the specific functions of S100A4.

Reviewer #3

Major comments:

2) The differential systemic versus mammary-specific effects of DTA-mediated S100A4 cell ablation are intriguing. The authors should address why the mammary fat pad appears unaffected.

Thank you for this comment. The role of S100A4+ cells in adipose tissue was previously reported (Zhang et al., 2018). Authors reported significantly smaller adipose tissue of S100a4-Cre;DTA mice (males and females), measured as the weight of the dissected fat pad. In our work, we measured the in-situ area of the fat pad, which appeared to be unaffected. It is possible that the volume (weight) of the fat pad would be different, however we do not have data to confirm / reject this hypothesis.

Are S100A4 expressing cells present during embryonic mammary development, or are they mainly postnatal? Would an inducible S100A4CreERT model lead to similar phenotypes, or might the timing of depletion influence the outcome? Discussing these points would reinforce the conclusions regarding the contribution of S100A4-expressing cells to mammary and nipple development and could also clarify the transient nature of the ductal branching phenotype.

S100A4-expressing cells are present during embryonic mammary development, too. Please, refer to the embryonic lineage-tracing time-points incorporated in the first version of the manuscript (Figure 5a and Figure S6a). Now, we have added Figure for Reviewers 1 corresponding to Figure S3 in the revised manuscript), which focuses on the embryonic nipple phenotype but also provides information on the presence of S100A4+ cells.

We agree that the use of inducible S100a4-CreERT model could potentially bring new insights toward developmental stage-specific roles of S100A4+ cells, and thus would be interesting to use in a follow-up study. Currently, such experiments are beyond our capacity.

Therefore, we have included a new subsection on Limitations of the study, where we comment:

“A major limitation of this study is that the timing of DTA-mediated cell depletion cannot be precisely defined in the constitutive mouse model employing S100a4-Cre because recombination may occur continuously following the initial expression of S100a4 (E8.518). This limitation could be overcome by usage of inducible S100a4-CreERT instead. With this approach, it could be more feasible to determine if the nipple deformity arises as a defect of embryonic development or postnatal morphogenesis.”

3) Although the authors attribute lactation failure primarily to defects in nipple architecture, the RNA seq data reveal downregulation of key milk production genes and luminal differentiation keratins, strongly suggesting impaired secretory activation. The authors should more explicitly discuss the relative contributions of epithelial functional maturation defects versus nipple structural abnormalities to the lactation failure observed upon S100A4+ cell depletion. Thank you for this comment. We believe that performing an immunofluorescence labeling of epithelial architecture (requested in the Minor comment 2) could bring more light into this. However, we deduce that secretory activation is not impaired, as the presence of the milk observed on in situ wholemounts, and H&E-stained alveoli (Figure 3d) implies luminal secretion of milk components. The observed phenotype of the lactating mammary gland strongly suggests there is a structural abnormality inhibiting the milk ejection.

The downregulation of key milk production genes and luminal keratins in the bulk RNA-seq data may be influenced by differences in tissue composition between samples. In control mice, more fully developed nipples and an extended ductal network likely contribute to a greater representation of differentiated luminal epithelial cells, thereby increasing the expression of these markers.

Minor comments:

1. Figure 1: Including an immunohistochemistry or immunofluorescence control confirming depletion of S100A4 expressing cells would strengthen the conclusions.

We have now included Figure for Reviewers 5 that corresponds to Figure S7 in the revised manuscript and comment on the results in sections Results (lines 169-171) and Discussion (lines 257-262).

In Results: “Interestingly, S100A4 antibody labeling revealed presence of S100A4+ cells in S100a4-Cre;DTA tissues (Figure S3b, Figure S7a,b).”

In Discussion: “Notably, we observed incomplete depletion of S100A4+ cells in the mammary gland and nipple. Interestingly, a study using the same S100a4-Cre;DTA mouse model reported complete S100A4+ cell depletion in the superficial layer of mandibular condyle48. This suggests that incomplete depletion of S100A4+ cells in nipple and mammary gland is due to tissue-specific dynamics, rather than lack of depletion efficiency, indicating a compensatory mechanism that can balance the cell loss.”

Figure for Reviewers 5 (Figure S7 in the revised manuscript): S100A4+ cells are found in S100a4-Cre;DTA nipple and mammary tissues. (a) Immunofluorescent labeling for S100A4 and vimentin on FFPE sections of DTA and S100a4-Cre;DTA L1 nipples. (b) Immunofluorescent labeling for S100A4 and smooth muscle actin on FFPE sections of DTA and S100a4-Cre;DTA L1 mammary gland. Scale bar = 100 µm.

Figure 3c: The histological defects more accurately reflect failure of secretory activation rather than "lactation failure" per se. The terminology should be refined to reflect this more precisely.

Thank you for this comment. As explained in the response to your major comment 3, we believe our results show that the secretory activation is conserved in S100a4-Cre;DTA lactating mice. We understand that “lactation failure” might be misleading terminology, as the production of the milk is conserved as well. We therefore change the phrasing into “nursing defect” (line 51, 73, 83), as this could reflect the phenotype most precisely.

**Referee cross-comenting**

I agree with the Reviewer, the authors do not need to do knockout experiments in the revised manuscript. However, it would be great if they could address my comment in the discussion.

Reviewer #3 (Significance (Required)):

This is an important study for mammary developmental biology, addressing the relatively understudied mechanisms that govern nipple development at the stromal-epithelial interface, and the determinants of lactational performance. A major strength is the elegant integration of DTA-mediated cell ablation, advanced imaging, lineage tracing, and transcriptomics to uncover previously uncharacterised roles for S100A4-expressing stromal populations in shaping nipple morphology and function. The work lays a foundation for future studies into nipple biology and pathologies and mechanisms underlying successful lactation.

Although the study is already mature, it could be further strengthened by incorporating more specific genetic models, such as inducible S100A4CreERT or S100A4 gene knockout/knockdown approaches.

Thank you for appreciation of our work.

4. Description of analyses that authors prefer not to carry out

Reviewer #1

Major Comment 1.

It is rather difficult to conclude whether the observed nipple phenotype reflects an early embryonic/prepubertal defect in establishing the nipple stroma, is caused by a constitutive response to ongoing cell death, or a response to continuous DTA expression (or a combination of some of these). The data raise a couple of additional questions: Is there a nipple phenotype at 3 wk of age?...

Unfortunately, we cannot provide data on 3 weeks old mice because we did not collect such samples before and we had to terminate our mouse colony due to an infection in the animal house (mouse line reanimation is possible because we had stored sperm of the mouse line but it would take a lot of time and resources). Nevertheless, we tried to address this comment by providing other relevant available data (see Figure for Reviewers 1).

Reviewer #2

Major Comment 3.

In Fig S1c, d and lines 93-96, the authors investigated the estrus cycles to determine the potential cause of lactation failure. The data was presented as the number of mice in each stage. A more intuitive approach would be to follow the same mice for two to three cycles and observe the duration of each stage.

We agree that the suggested approach would be more accurate in determining truly cycling females. Unfortunately, we cannot perform this experiment currently because we do not have these mice alive anymore. Nevertheless, because the S100a4-Cre;DTA females bore pups, they had cycled and were fertile.

Reviewer #3

Major comment 1.

While the S100A4Cre::DTA model is powerful for evaluating the roles of S100A4 expressing cells, the authors should discuss the potential outcomes of using S100A4 knockout or knockdown approaches. If the authors have such data available, this could help distinguish phenotypes caused by loss of S100A4 function itself from those arising due to ablation of S100A4 expressing cell populations and would add mechanistic depth to the study.

We thank the Reviewer for this insightful suggestion. We agree that genetic approaches targeting S100A4 function (e.g., knockout or knockdown) could, in principle, help disentangle cell-autonomous effects of S100A4 from those resulting from the loss of S100A4-expressing cell populations. However, we would like to clarify that the primary objective of our study is to investigate the functional contribution of S100A4⁺ stromal cells at the population level, rather than to dissect the molecular function of S100A4 protein per se. In this context, the S100A4-Cre;DTA model provides a well-established and appropriate strategy to ablate this cell population and assess its role in tissue development. Importantly, S100A4 is not only a functional protein but also a widely used marker of a heterogeneous stromal cell population. Genetic ablation of S100A4 itself would not eliminate these cells, and may result in relatively subtle or compensable phenotypes due to functional redundancy within the S100 protein family or context-dependent roles of S100A4. Therefore, such approaches would address a distinct biological question and may not directly recapitulate the phenotypes observed upon cell ablation.

References

Eisen, E. J., & Durrant, B. S. (1980). Genetic and Maternal Environmental Factors Influencing Litter Size and Reproductive Efficiency in Mice. Journal of Animal Science, 50(3), 428–441. https://doi.org/10.2527/jas1980.503428x

Ren, Y. A., Monkkonen, T., Lewis, M. T., Bernard, D. J., Christian, H. C., Jorgez, C. J., Moore, J. A., Landua, J. D., Chin, H. M., Chen, W., Singh, S., Kim, I. S., Zhang, X. H. F., Xia, Y., Phillips, K. J., MacKay, H., Waterland, R. A., Cecilia Ljungberg, M., Saha, P. K., … Richards, J. A. S. (2019). S100a4-Cre–mediated deletion of Ptch1 causes hypogonadotropic hypogonadism: Role of pituitary hematopoietic cells in endocrine regulation. JCI Insight, 4(14). https://doi.org/10.1172/jci.insight.126325

Tuwatnawanit, T., Wessman, W., Belisova, D., Sumbalova Koledova, Z., Tucker, A. S., & Anthwal, N. (2025). FSP1/S100A4-Expressing Stem/Progenitor Cells Are Essential for Temporomandibular Joint Growth and Homeostasis. Journal of Dental Research, 104(5), 551–560. https://doi.org/10.1177/00220345251313795

Zhang, R., Gao, Y., Zhao, X., Gao, M., Wu, Y., Han, Y., Qiao, Y., Luo, Z., Yang, L., Chen, J., & Ge, G. (2018). FSP1-positive fibroblasts are adipogenic niche and regulate adipose homeostasis. PLoS Biology, 16(8). https://doi.org/10.1371/journal.pbio.2001493

Author Response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

Mancl et al. present a comprehensive integrative study combining cryo-EM, SAXS, enzymatic assays, and molecular dynamics (MD) simulations to characterize conformational dynamics of human insulin-degrading enzyme (IDE). In the revised manuscript, the study now also includes time-resolved cryo-EM and coarse-grained MD simulations, which strengthen the mechanistic model by revealing insulin-induced allostery and β-sheet interactions between IDE and insulin. Together, these results expand the original mechanistic insight and further validate R668 as a key residue governing the open-close transition and substrate-dependent activity modulation of IDE.

Strengths:

The authors have substantially expanded the experimental scope by adding time-resolved cryo-EM data and coarse-grained MD simulations, directly addressing requests for mechanistic depth and temporal insight. The integration of multiple resolution scales (cryo-EM heterogeneity analysis, all-atom and coarse-grained MD simulations, and biochemical validation) now provides a coherent description of the conformational transitions and allosteric regulation of IDE. The addition of Aβ degradation assays strengthens the claim that R668 modulates IDE function in a substrate-specific manner. Finally, the manuscript reads more clearly: figure organization, section headers, and inclusion of a new introductory figure make it accessible to a broader audience. Overall, the revision reinforces the conceptual advance that the dynamic interdomain motions of IDE underlie both its unfoldase and protease activities and identifies structural motifs that could be targeted pharmacologically.

Weaknesses:

While the authors acknowledge that future studies on additional IDE substrates (e.g., amylin and glucagon) are warranted, such experiments remain outside the present scope. Their absence modestly limits the generalization of the R668 mechanism across all IDE substrates. Despite improved discussion of kinetic timescales and enzyme-substrate interactions, experimental correlation between MD timescales and catalysis remains primarily inferential. The moderate local resolution of some cryo-EM states (notably O/pO) continues to limit atomic interpretation of the most flexible regions, though the authors address this carefully.

Reviewer #2 (Public review):

Summary:

The manuscript describes various conformational states and structural dynamics of the Insulin degrading enzyme (IDE), a zinc metalloprotease by nature. Both open and closed state structures of IDE have been previously solved using crystallography and cryo-EM which reveal a dimeric organization of IDE where each monomer is organized into N and C domains. C-domains form the interacting interface in the dimeric protein while the two N-domains are positioned on the outer sides of the core formed by C-domains. It remains elusive how the open state is converted into the closed state but it is generally accepted that it involves large-scale movement of N-domains relative to the C-domains. Authors here have used various complementary experimental techniques such as cryo-EM, SAXS, size-exclusion chromatography and enzymatic assays to characterize the structure and dynamics of IDE protein in the presence of substrate protein insulin whose density is captured in all the structures solved. The experimental structural data from cryo-EM suffered from high degree of intrinsic motion amongst the different domains and consequently, the resultant structures were moderately resolved at 3-4.1 Å resolution. Total five structures were generated in the originally submitted manuscript using cryo-EM. Another cryo-EM reconstruction (sixth) at 5.1Å resolution was mentioned after first revision which was obtained using time-resolved cryo-EM experiments. Authors have extensively used Molecular dynamics simulation to fish out important inter-subunit contacts which involves R668, E381, D309, etc residues. In summary, authors have explored the conformational dynamics of IDE protein using experimental approaches which are complimented and analyzed in atomic details by using MD simulation studies. The studies are meticulously conducted and lay ground for future exploration of protease structure-function relationship.

Comments after first peer-review:

The authors have addressed all my concerns, and have added new data and explanations in terms of time-resolved cryo-EM (Fig. 7) and upside simulations (Fig. 8) which in my opinion have strengthened the merit of the manuscript.

We are grateful for the dedication and constructive feedback provided by the editors and reviewers. We have revised our manuscript according to the suggestions by both reviewers.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The new version of the manuscript reads exceedingly well and the corrections the authors have made during their revision made the manuscript much easier to read and digest than the first version. Below are minor details that may be corrected:

Abstract:

Line 45-47: "IDE is known to transition between a closed state, poised for catalysis, and an open state, able to release cleavage products and bind a new substrate." (consider adding a)

Fixed

Line 48-50: "Combining cryo-EM heterogeneity analysis with all-atom molecular dynamics (MD) simulations, we identified the structural basis and key residues for IDE conformational dynamics that were not previously revealed by IDE static structures." (consider adding previously)

Changed

Line 52-54: "Our small-angle X-ray scattering analysis and enzymatic assays of an R668A mutant indicate a profound alteration of conformational dynamics and catalytic activity." (consider adding analysis)

Changed

Line 54: Consider leaving out "Upside" in the abstract (to avoid confusion when reading the abstract) and leave it to be introduced in the introduction when Upside MD simulations are first mentioned.

Changed

Results:

Figure 5D: There seems to be an error in the legend for Figure 5D. It says "... presence of varying amounts of insulin", but this must be Aβ1-40. Please add info on whether the replicates are technical or biological.

The legend has been revised as suggested.

Line 125: Consider switching the order of "here" and "we"

“here” has been removed.

Line 128: Replace "5" with "five"

Changed

Line 137: Replace "when insulin is present" with "in the presence of insulin"

Changed

Line 228: Replace "5" and "6" with "five " and "six"

Changed

Line 229: Consider adding the word "form": "First, the open subunits did not close to form a singular structure."

We have adjusted the sentence to read “close to a singular consensus structure”

Line 327: Replace "2" with "two"

Changed

Line 276: Consider replacing "Conversely" with a more suitable connecting term as it implies that the observation presented in the two sentences are reverse or rephrase what is being compared. Is it the fact there is a dose dependency or not between the substrates or is it the actual kinetic parameters that are described. I just don't think conversely is fair with the current formulation as "the R668A mutant did not exhibit a dose-dependent response to the presence of Aβ" not that the Ki is reduced for WT compared to the R668A construct when looking at Aβ.

The connecting term has been removed completely, beginning the sentence with “When Abeta…”

Line 359: Replace "6" with "six"

Changed

Consider getting rid of possessive apostrophes to keep a formal tone, e.g. lines 211 (cryoSPARC's), 259 (IDE's) and 382 (IDE's). Exception to this is Alzheimer's disease.

All instances of possessive apostrophes, aside from Alzheimer’s, have been replaced alter more formal wording.

Figure 7 supplement 1: The color scheme for the local resolution is missing the unit (Å).

This has been corrected.

Finally, the supplementary videos illustrating IDE conformational dynamics are difficult to interpret and somewhat redundant in their current form. The transitions occur very rapidly, making it hard to appreciate the described motions, and the uniform coloring of IDE further limits visual clarity. I apologize for not including this point in my initial review. I recommend either removing the videos or re-rendering them to improve interpretability, for example by slowing down the motion and applying the same domain color scheme introduced in the new Figure 1 (and used in the MD trajectory video). This would greatly aid readers in connecting the descriptions in the text to the visual representations in the movies.

Figure 3 videos 1-4 were slowed down, simplified, and recolored to improve clarity.

Reviewer #2 (Recommendations for the authors):

Comments after first revision for authors:

Thanks a ton to the authors for the detailed explanation on my comments. I believe the discussions will help a large group of audience, especially the non-experts. Please address the minor comment below:

Minor comment:

Please update Supplementary file 1 (Cryo-EM data collection, refinement, and validation statistics) regarding the new volume obtained by time-resolved cryo-EM. Kindly also check line 47 in the abstract: "Here, we present five cryo-EM structures" , which may need an update (six structures and resolution 3.0-5.1 Å) or rephrase the sentences accordingly. If similar instances are found in the manuscript, where list of all the structures are mentioned together, please update accordingly if necessary.

The cryo-EM statistics for the time-resolved cryo-EM are shown in supplementary file 2 to differentiated two datasets. The abstract has been changed, as has line 149.

Author Response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

Age-related synaptic dysfunction can have detrimental effects on cognitive and locomotor function. Additionally, aging makes the nervous system vulnerable to late-onset neurodegenerative diseases. This manuscript by Marques et al. seeks to profile the cell surface proteomes of glia to uncover signaling pathways that are implicated in age-related neurodegeneration. They compared the glial cell-surface proteomes in the central brain of young (day 5) and old (day 50) flies and identified the most up- and down-regulated proteins during the aging process. 48 genes were selected for analysis in a lifespan screen, and interestingly, most sex-specific phenotypes. Among these, adult-specific pan-glial DIP-β overexpression (OE) significantly increased the lifespan of both males and females and improved their motor control ability. To investigate the effect of DIP-β in the aging brain, Marques et al. performed snRNA-seq on 50-day-old Drosophila brains with or without DIP-β OE in glia. Cortex and ensheathing glia showed the most differentially expressed genes. Computational analysis revealed that glial DIP-β OE increased cell-cell communication, particularly with neurons and fat cells.

Strengths:

(1) State-of-the-art methodology to reveal the cell surface proteomes of glia in young and old flies.

(2) Rigorous analyses to identify differentially expressed proteins.

(3) Examination of up- and down-regulated candidates and identification of glial-expressed mediators that impact fly lifespan.

(4) Intriguing sex-specific glial genes that regulate life span.

(5) Follow-up RNA-seq analysis to examine cellular transcriptomes upon overexpression of an identified candidate (DIP-β).

(6) A compelling dataset for the community that should generate extensive interest and spawn many projects.

Weaknesses:

(1) DIP-β OE using flySAM:

(a) These flies showed a larger increase in lifespan compared to using UAS-DIP-β (Figure 2 C, D). Do the authors think that flySAM is a more efficient way of OE than UAS? Also, the UAS construct would be specific to one DIP-β isoform, while flySAM would likely express all isoforms. Could this also contribute to the phenotypes observed?

We agree with the reviewer that both can contribute to the different lifespan effect. In the original paper presenting flySAM1.0 and flySAM 2.0 (Jia et al., 2018), the authors first tested how flySAM1.0 overexpression (OE) phenotypes compare to several VPR (CRISPRa) and UAS:cDNA OE lines. They found that flySAM1.0 reliably outperforms (i.e., produces stronger OE phenotypes) than VPR in most cases, and produces OE phenotypes that are comparable (i.e., generally equivalent) to UAS:cDNA (Jia et al., 2018). After determining how flySAM1.0 performance compares to VPR and UAS:cDNA, the authors next tested if flySAM2.0 also outperforms VPR; they found that like flySAM1.0, flySAM2.0 outperforms VPR in most cases (Jia et al., 2018). In general, the data suggest that we should expect comparable overexpression phenotypes for our flySAM2.0 and UAS:cDNA lines.

We chose to proceed with the DIP-β flySAM line for the climbing assays and snRNA-seq, as it gave a stronger lifespan effect and we thought it was likely to be the more robust OE line. While our glial cell-surface proteomics initially identified DIP-β isoform C as the candidate, it is possible that other DIP-β isoforms were also present (such as isoform F, which is identical in polypeptide sequence to isoform C) (FlyBase). Ultimately, we believe that the larger increases in lifespan observed for DIP-β flySAM are likely because flySAM targets all isoforms, whereas UAS:cDNA lines target only one isoform. Importantly, our UAS- DIP-β line was specific to DIP-β isoform C, which is the same isoform that was identified by our proteomics.

We have made clarifications in the manuscript to address these comments.

(b) The Glial-GS>DIP-β flySAM flies without RU-486 have significantly shorter lifespans (Figure 2C) than their UAS-DIP-β counterparts. flySAM is lethal when expressed under the control of tubulin-GAL4 (Jia et al. 2018), likely due to the toxicity of such high levels of overexpression. Is it possible that a larger increase in lifespan is due to the already reduced viability of these flies?

This is a good point. The flySAM lines do exhibit a shorter baseline lifespan compared to the traditional UAS lines. This is likely due to the specific genetic background of the flySAM transgenic insertions, or a low level of "leaky" expression, as previously noted in the literature (Jia et al., 2018).

However, we believe that the lifespan extensions we observed for DIP-β flySAM is a robust biological effect, rather than an artifact of reduced viability for the following reasons. First, by utilizing the GeneSwitch (GS) system, we can compare the lifespan of flies with the exact same genetic background (+/- RU-486). This ensures that the extension we report is specifically due to the induction of the transgene, rather than a comparison between disparate lines with different basal fitness levels. Second, if the lifespan extensions merely represented a recovery from lower baseline viability, we would expect to see similar improvements across other flySAM lines in our screen. However, DIP-β was the only candidate across our screen that significantly increased lifespan in both sexes (Extended Data Figs. 7 & 8). Third, the lifespan-extending effect of DIP-β was independently confirmed using a traditional UAS-cDNA line, which importantly does not share the same baseline viability issues as the flySAM lines.

(c) Statistics: It is stated in the Methods that "statistical methods used are described in the figure legend of each relevant panel." However, there is no description of the statistics or sample sizes used in Figure 2.

We have updated the figure legends for Figure 2 to include the missing statistical details and sample sizes.

Specifically, for Fig. 2A: The reviewer is correct that with only two replicates of each time point (5d vs. 50d) in the initial proteomic screen, traditional p-value calculations lack the necessary power for meaningful interpretation. We have revised the legend to clarify that this panel represents a discovery-based screen. Candidates were selected based on biological relevance and specific enrichment thresholds to narrow the 872 proteins down to the 48 top candidates for screening (we were initially aiming to identify approximately 50 candidate genes for screening). For Fig. 2B: We have updated the legend to detail the parameters used for the Gene Ontology (GO) enrichment analysis.

(2) Figure 3: The authors use a glial GeneSwitch (GS) to knock down and overexpress candidate genes. In Figure 3A, they look at glial-GS>UAS-GFP with and without RU. Without RU, there is no GFP expression, as expected. With RU, there is GFP expression. It is expected that all cell body GFP signal should colocalize with a glial nuclear marker (Repo). However, there is some signal that does not appear to be glia. Also, many glia do not express GFP, suggesting the glial GS driver does not label all glia. This could impact which glia are being targeted in several experiments.

We thank the reviewer for this careful observation regarding the expression pattern of the GSG3285-1 line and acknowledge that the overlap between this driver and the Repo-positive cells is not absolute.

Our selection of this specific GeneSwitch line was based on several critical experimental considerations: 1) To minimize background toxicity. We initially tested multiple Repo-GeneSwitch lines; however, we found they exhibited significant, genotype-dependent lifespan reductions upon RU486 administration, even in control crosses. This baseline toxicity confounded the interpretation of any potential lifespan effects. GSG3285-1 was chosen for this study, as it provided a robust control baseline and didn’t show lifespan effects with RU486 treatment in multiple control lines. This is essential for lifespan studies. 2) The driver breadth and specificity. As noted in its original characterization (Nicholson et al., 2008) and a later study (Catterson et al. 2023), GSG3285-1 is characterized as a pan-glial driver, though it may include a small population of sensory neurons. Furthermore, while Repo is a standard glial marker, its antibody does not label all glial subtypes with equal intensity. The "non-overlapping" signal observed in Figure 3A may reflect this staining bias. 3) The expression mosaicism. The fact that some glial cells do not show GFP expression suggests a degree of mosaicism, which is common to many GeneSwitch lines (Osterwalder et al., 2001). While we acknowledge this means our manipulations may target a broader subset — rather than every single glial cell — the fact that we still observed significant lifespan effects across two independent platforms (UAS and CRISPRa) suggests that the targeted population is sufficient to mediate these systemic effects.

We have added a clarifying statement to contextualize the choice of the GSG3285-1 driver and its relationship to the Repo population.

(3) It is interesting that sex-specific lifespan effects were observed in the candidate screen.

(a) The authors should provide a discussion about these sex-specific differences and their thoughts about why these were observed.

We agree that the sex-specific effects observed in our lifespan screen are one interesting aspect of this study. We have added a dedicated section to the Discussion exploring these differences from both a technical and biological perspective.

On the technical side, the GeneSwitch inducer, RU486, can have sex-specific effects on metabolism and lifespan, depending on the nutritional environment (Dos Santos & Cocheme, 2024). Specifically, RU486 has been shown to counteract the lifespan-shortening effects of mating in females, an effect that is less pronounced in males (Landis et al., 2015; Tower et al., 2017). While we optimized our media and used the GSG3285-1 line to minimize these baseline effects, it remains possible that certain genotypes exhibited a sex-specific sensitivity to the inducer itself. Beyond the technical considerations, sex differences in aging are well-documented in Drosophila and other organisms (Regan et al., 2016; Austad & Fischer, 2016). Male and female flies exhibit distinct transcriptional trajectories and metabolic shifts as they age. Furthermore, recent studies have highlighted that glial function and the neuroinflammatory landscape can differ significantly between sexes, which may dictate how a specific genetic manipulation impacts the aging process in a sex-dependent manner (PMID: 40951920). While our screen identifies DIP-β as a rare candidate that extends lifespan in both sexes, the prevalence of female-specific hits in our data suggests that the female "aging program" may be more plastic or responsive to the specific glial pathways we targeted. These observations provide a valuable foundation for future studies into the mechanisms of sex-specific neuroprotection.

(b) The authors should also provide information regarding the sex of the flies used in the glial cell surface proteome study.

It is a mixture of half male and half female flies. This information has been added to the main text, Fig. 1, and to the methods section.

(c) Also, beyond the scope of this study, examining sex-specific glial proteomes could reveal additional insights into age-related pathways affecting males and females differentially.

Agreed, this would be a great idea for future studies.

(4) The behavioral assay used in this study (climbing) tests locomotion driven by motor neurons. The proteomic analysis was performed with the adult brain, which does not include the nerve cord, where motor neurons reside. While likely beyond the scope of this study, it would be informative to test other behaviors, including learning, circadian rhythms, etc.

We thank the reviewer for this insightful point. While our initial proteomic screen focused on the adult central brain, our behavioral validation used a pan-glial driver, which targets glia throughout the entire nervous system, including the ventral nerve cord (VNC). We have addressed the reviewer's comment as below:

Additional behavioral data: As suggested, we performed Drosophila Activity Monitoring (DAM) assays to evaluate circadian locomotor rhythms in 50-day-old DIP-β overexpression flies compared to negative controls. Interestingly, we did not detect significant changes in circadian activity at this time point.

The difference between our climbing and circadian results highlights the complexity of age-related decline. In Drosophila, locomotor performance (i.e., climbing) and circadian coordination often decouple. For example, specific isoforms of human Tau (hTau) can induce severe cognitive and neurodegenerative deficits without affecting lifespan or motor coordination in the same manner (Sealey et al., 2017). Furthermore, motor-specific defects can emerge independently of systemic lifespan changes, as seen in certain SOD1 models of ALS (Hirth, 2010). It is possible that the 50-day timepoint represents a specific window where motor coordination is improved by DIP-β, while circadian circuits — governed by distinct glial-neuronal interactions — remain largely unaffected, or require a different temporal window for observation.

We agree that identifying the specific glial populations (central brain vs VNC) responsible for the improved climbing would be highly informative. While the current study establishes the pro-longevity effect of DIP-β, future work utilizing in-situ proteomics on the fully intact CNS (including the VNC) or specific VNC will be essential to map the stereotyped progression of these effects across the peripheral and central nervous systems.

(5) It is surprising that overexpressing a CAM in glia has such a broad impact on the transcriptomes of so many different cell types. Could this be due to DIP-β OE maintaining the brain in a "younger" state and indirectly influencing the transcriptomes? Instead of DIP-β OE in glia directly influencing cell-cell interactions? Can the authors comment on this?

We agree that the observed changes likely represent a combination of direct cell-cell interactions and a broader, more indirect maintenance of a "younger" physiological state.

Direct: Among the DIP family, DIP-β exhibits some of the strongest and most promiscuous binding affinities, interacting with a wide array of partners including Dpr6, 8, 9, 15, and 21 (Cosmanescu et al., 2018; Sergeeva et al., 2020). This biochemical flexibility allows DIP-β to potentially interface with a much broader range of neuronal subtypes than other DIP family members, such as DIP-δ, which exclusively binds Dpr12 and did not extend lifespan in our screen. It is possible that by overexpressing DIP-β, we may be partially compensating for the global downregulation of CAMs that typically occurs during aging, thereby preserving essential glial-neuronal communication integrity.

Indirect: By maintaining these primary glial functions and communication activities, DIP-β overexpression likely delays the overall "aging" of the brain. This preservation of neural health can have downstream effects on systemic physiology, such as the improved glia-fat body communication we observed in 50-day-old flies. In this model, the broad transcriptomic shifts are not necessarily all direct targets of DIP-β, but rather a signature of a brain that has successfully avoided the catastrophic breakdown of homeostasis typically seen in aged wild-type flies.

We have expanded the Discussion to clarify this distinction, adding that DIP-β likely acts as a "scaffold" or “bridge” for maintaining a younger brain state, which in turn preserves multi-organ communication.

Reviewer #2 (Public review):

This manuscript presents an ambitious and technically innovative study that combines in situ cell-surface proteomics, functional genetic screening, and single-nucleus RNA sequencing to uncover glial factors that influence aging in Drosophila. The authors identify DIP-β as a glial protein whose overexpression extends lifespan and report intriguing sex-specific differences in lifespan outcomes. Overall, the study is conceptually compelling and offers a valuable dataset that will be of considerable interest to researchers studying glia-neuron communication, aging biology, and proteomic profiling in vivo.

The in-situ proteomic labeling approach represents a notable methodological advance. If validated more extensively, it has the potential to become a widely used resource for probing glial aging mechanisms. The use of an inducible glial GeneSwitch driver is another strength, enabling the authors to carefully separate aging-relevant effects from developmental confounds. These technical choices meaningfully elevate the rigor of the study and support its central conclusions. The discovery of new candidate genes from the proteomics pipeline, including DIP-β, is intriguing and opens new avenues for understanding glial contributions to organismal lifespan. The observation of sex-specific lifespan effects is particularly interesting and warrants further exploration; the study sets the stage for future work in this direction.

At the same time, several areas would benefit from clarification or additional analysis to fully support the manuscript's claims:

(1) The manuscript frequently refers to "improved" or "increased" cell-cell communication following DIP-β overexpression, but the meaning of this term remains somewhat vague. Because the current analysis relies largely on transcriptomic predictions, it would be helpful to define precisely what metric is being used, e.g., increased numbers of predicted ligand-receptor interactions, enrichment of specific signaling pathways, or altered expression of communication-related components. Strengthening the mechanistic link between DIP-β, cell-cell communication, and lifespan extension, potentially through targeted validation of specific glial interactions, would substantially reinforce the interpretation.

We agree that a more precise description of “improved” or “increased” cell-cell communication is necessary.

Our conclusion that DIP-β overexpression is associated with “increased” cell-cell communication is based on the quantification of our CCC scores, which was performed using FlyPhoneDB2, a computational tool used to estimate cell-cell signaling from single-cell RNA-sequencing data (Liu et al., 2021; Qadiri et al., 2025). To infer cell-cell signaling, FlyPhoneDB2 and its predecessor, FlyPhoneDB, calculate “interaction scores,” comparing the expression levels of a curated list of ligand-receptor pairs between cell types (Liu et al., 2021; Qadiri et al., 2025). For example, if we detect a ligand in cell type A and its receptor in cell type B in DIP-β overexpression flies but didn’t detect both ligand and receptor in control flies, the CCC score is increased by 1. FlyPhoneDB2 additionally enables users to estimate signaling activity by also taking into consideration the expression of downstream reporter genes (Qadiri et al., 2025).

“Improved cell-cell communication” is our interpretation based on the CCC analysis. It is important to note that the metric being used here (increased CCCs) is the number of predicted ligand-receptor interactions, and that our CCC analysis was based entirely on inferences from snRNA-seq data. We have added further clarification to our manuscript, which now further expands on the results of our CCC analysis (i.e., the increased expression for 61% and decreased expression for 39% of ligand-receptor pairs we observed in our DIP-β overexpression group, compared to our negative control), which ultimately led us to conclude that DIP-β overexpression is associated with improved cell-cell communication.

(2) The lifespan screen is central to the paper, and clearer visualization and contextualization of these results would significantly improve the manuscript's impact. For example, Figure 3D is challenging to interpret in its current form. More explicit presentation of which manipulations extend lifespan in each sex, along with effect sizes and significance values, would provide clarity. Including positive controls for lifespan extension would also help contextualize the magnitude of the observed effects. The reported effects of DIP-β, while promising, are modest relative to baseline effects of RU feeding, and a discussion of this would help appropriately calibrate the conclusions.

We appreciate the reviewer’s suggestion to improve the clarity of the lifespan screen results. We have significantly revised Figures 3D, 3E, and 3F to provide a more intuitive summary of the candidate gene manipulations. Figures 3D and 3E now explicitly include the effect sizes and p-values for each candidate gene, broken down by sex. We also added a new Figure 3G with a visual layout that has been streamlined to allow for quick identification of manipulations that successfully extended lifespan.

The reviewer raises an important point regarding the use of positive controls to calibrate the magnitude of lifespan extension. We carefully considered adding a standard control (such as Rapamycin treatment); however, we opted against it for several methodological reasons:

As noted in the literature, the magnitude of lifespan extension from standard controls can vary drastically depending on genetic background and lab environment. For instance, Rapamycin-induced extension ranges from ~10% (Schinaman et al., 2019), to over 80% (Landis et al., 2024). We felt that adding a single positive control might provide a false sense of "calibration" rather than a true universal benchmark.

To ensure the robustness of our findings, we instead employed a dual-validation strategy. We confirmed the lifespan-extending effects of our candidates using both traditional UAS:cDNA and CRISPR-based overexpression. The fact that two independent genetic systems yielded consistent results provides strong internal evidence for the reported effects.

We acknowledge that the effects of DIP-β are modest when compared to the baseline impact of RU486 feeding. We have added a section to the Discussion addressing this. While the effects are subtle, their reproducibility across different overexpression platforms suggests they are biologically relevant, even if they do not reach the dramatic shifts seen in some caloric restriction or drug-based models.

We have further addressed this in the results section.

(3) Several figures would benefit from improved labeling or more detailed legends. For instance, the meaning of "N" and "C" in Figure 1D is unclear; Figure 3A should clarify that Repo is a glial marker; and Figure 5C appears to have truncated labels. Reordering certain panels (e.g., moving control data in Figure 4A-B) may also improve narrative flow. These refinements would greatly aid reader comprehension.

We have modified and improved the labeling of these figures to increase the clarity. For Fig. 1D, we added the explanation to the Figure legends. In brief, in the Tandem Mass Tag (TMT) isobaric labeling system, 128N is one of many channels (126, 127N, 127C, 128N, 128C, etc.) used to index and compare up to 18 samples simultaneously, improving throughput and reducing missing values.

Fig. 3A has been updated to clarify that Repo is the glial marker. Fig. 4A-D have been reordered so that the DIP- β lifespan results are presented before the control lifespan, which hopefully improves the narrative flow of this figure. The Fig. 4 references in the manuscript have also been updated to match these changes. Additionally, Fig. 5C has been updated to include the truncated x-axis and y-axis labels.

(4) A few claims would be strengthened by more specific references or acknowledgment of alternative interpretations. Examples include the phenoxy-radical labeling radius, the impact of H₂O₂ exposure, and the specificity of neutravidin. Additionally, downregulation of synapse-related GO terms may reflect age-related transcriptional changes rather than impaired glia-neuron communication per se, and this possibility should be recognized. The term "unbiased" to describe the screen may also be reconsidered, given the preselection of candidate genes.

These are good suggestions. We have added references for the phenoxy-radical labeling radius (Durojaye, 2021), the impact of H₂O₂ exposure (J. Li et al., 2021), and the binding specificity of neutravidin (J. Li et al., 2021). We have also removed the term “unbiased” from our manuscript.

Regarding the request to further address the downregulation of synapse-related GO terms, we believe this indicates a lack of clarity on our part. We did not intend to suggest that our GO analyses, which were based on our proteomics data, were necessarily indicative of impaired neuron-glia communication. Our conclusions regarding altered neuron-glia communication have come from our later snRNA-seq data and analyses. Inspired by this comment, we agree that our differential gene analysis may reflect transcriptional changes rather than impaired glia-neuron communication. We have added such alternative interpretation.

(5) Clarifying the rationale for focusing on central brain glia over optic-lobe glia would be useful. 

Agreed! As the intended focus of this study was the more general changes occurring during normal brain aging, we chose to focus on the central brain for our glial cell-surface proteomics, which is responsible for most of the brain’s higher order functions, including learning and memory, signal integration, behavior, etc. As the optic lobes account for approximately half of all neurons in the adult Drosophila brain and are specialized to process visual stimuli (Robinson et al., 2025), we were concerned that including the optic lobes in our glial cell-surface proteomics could strongly bias our findings towards age-related changes in visual function, rather than the more general changes we intended to focus on. Such clarification has been added to the results section (Quantitative comparison of young and old proteomes).

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Line 62: Can the authors expand on "several changes"?

We have added a sentence expanding upon this in the manuscript draft.

(2) Line 137: Can the authors provide a reference for the phenoxyl radical half-life?

Thanks for catching this. We’ve added our reference for the phenoxyl radical half-life.

(3) Figure 1B: The authors state that neutravidin stained glia; however, there is no glial marker (e.g., anti-Repo) in this panel.

We acknowledge the reviewer’s point. The lack of anti-Repo staining in Figure 1B is due to the requirements of the Neutravidin-Alexa 647 detection method. Because this procedure bypasses traditional primary and secondary antibody incubation to preserve the biotin signal, co-staining with Repo was not technically feasible. Nevertheless, we utilized the Repo-GAL4 driver to express UAS-CD2-HRP; since this driver is well-documented and specific to glial cells, the Neutravidin signal serves as a functional readout of the targeted glial population.

(4) Line 254: There is no Figure 2D.

We’ve corrected this to Fig. 2C.

(5) Lines 390-396: No reference to the respective figures.

We’ve made a couple corrections to reference all the respective figures.

(6) Figure 5C: The X-axis is cut off.

This has been corrected.

Reviewer #2 (Recommendations for the authors):

Minor inconsistencies (e.g., figure references-line 254 references "Figure 2D" where none exists) should be corrected.

We’ve corrected this to Fig. 2C.

Author Response:

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

Reviewer #1 (Public review):

Genetically encoded fluorescent proteins expressed in specific cell types allow recognising them in vivo and, if the protein is a functional indicator, as in the case of genetically encoded calcium indicators (GECIs), to record activity from the same cellular ensemble. Ideally, if proteins (fluorophores) have perfectly distinct spectral properties, signals can be distinguished from as many cell types as the number of employed fluorophores. In practice, fluorescent proteins have non-negligible crosstalk both in absorption and emission bands. In addition, fluorescence contribution of each fluorophore normally varies from cell to cell and therefore spectral properties of cells expressing two or more proteins are different. The work of Phillips et al. addresses this challenge. The authors present an approach defined as "Neuroplex", allowing identification of up to nine cell types from the same number of fluorophores. The fingerprint of each cell is then associated with functional fluorescence from the GECI GCaMP, allowing recording calcium activity from that specific cell. The method is implemented in vivo using head-mounted miniscopes.

The authors used a mouse line expressing GCaMP in cortical pyramidal neurons and developed an experimental pipeline. First, they injected the nine AAV viruses, causing expression of fluorophores in a different brain area. The idea was not to image that area, but a non-infected medial prefrontal cortex (mPFC) section where neurons could be infected by their axons projecting in an injected area, in this way being identified by their targeting region(s). A GRIN lens, allowing spectral analysis, was mounted in the mPFC section, and GCaMP fluorescence was then recorded during behavioural tasks and analysed to identify regions of interest (ROIs) corresponding to neuron somata. After functional imaging, the head of the mouse was fixed, spectral analysis was performed, and after necessary correction for chromatic distortions, the fluorophore contribution was determined for each ROI (neuron) from where GCaMP signals were detected. Notably, the procedures for estimation and correction of chromatic aberration and light transmission (described in Figure 2) were a major challenge in their technical achievements. The selection of the nine fluorophores was another big effort. This was done by combining computer simulations and direct measurement of spectra from individual proteins expressed in HEK293 cells. It is important to say that the authors could simulate arbitrary combinations of two or more different fluorophores and evaluate the ability of their algorithm to detect the correct proteins against wrong estimations of false-negative (absence of an expressed protein) or false-positive (presence of a non-expressed protein). Not surprisingly, this ability decreases with the level of GCaMP expression. The authors underline that most errors were false-negatives, which have a milder impact in terms of result interpretation, but the rate of false positives was, nevertheless, relevant in detecting a second fluorophore from a cell expressing only one protein. The experimental profiles of fluorophores were dependent both on the specific fluorescent protein and on the projecting area, and the distribution of double-labelled did not match anatomical evidence. This result should be taken as the limitation of the present pioneering experiments, presented as proof-of-principle of the approach, but Neuroplex may provide far improved precision under different experimental conditions.

In my view, the work of Phillips et al. represents a significant advance in the state-of-the-art of the field. The rigorous analysis of limitations in the use of Neuroplex must be considered an important guideline for future uses of this approach.

We appreciate the reviewer’s positive evaluation and thoughtful comments.

Reviewer #2 (Public review):

Summary:

The manuscript introduces Neuroplex, a pipeline that integrates miniscope Ca²⁺ imaging in freely moving mice with multiplexed confocal and spectral imaging to infer projection identities of recorded neurons. This technical approach is promising and could broaden access to projection-resolved population imaging. However, the core quantitative analyses apply a winner-take-all single-label assignment per neuron even when multiple fluorophores exceed threshold, with additional labels treated descriptively as "secondary hits." While the authors acknowledge and simulate dual labeling, the extent to which this single-label decision rule affects subtype fractions and behavioural comparisons remains uncertain without a multi-label (or probabilistic) sensitivity analysis and propagation of classification uncertainty.

We thank Reviewer #2 for the careful statistical perspective and focus on assignment strategy and uncertainty. Importantly, we emphasize that Neuroplex is presented as a methodological proof-of-principle, not as a definitive quantification of projection convergence.

Strengths:

(1) Conceptual advance and practicality: Decoupling acquisition from identity readout constitutes an innovative approach that is, in principle, applicable in laboratories currently using single-color miniscopes.

(2) Engineering thoroughness: The manuscript offers detailed consideration of GRIN optics, spectral libraries, registration procedures, and simulations that address signal-to-noise ratio, background, and class imbalances.

(3) Immediate community value: If demonstrated to be robust, the pipeline could enable projection-resolved analyses without reliance on specialized multicolor miniscopes.

Weaknesses:

(1) Single-label assignment in the main analyses: When multiple fluorophores exceed threshold for a neuron/ROI, the workflow applies a winner-take-all rule and assigns a single label (the fluorophore with the largest standardized beta), while additional above-threshold fluorophores are retained only as "secondary hits." This is a reasonable specificity-first choice, but because cortical excitatory neurons can collateralize, collapsing dual-threshold ROIs to one identity may under-represent dual-projecting cells and could bias estimated subtype fractions and behavioural comparisons.

We thank the reviewer for raising this important conceptual point.

We agree that cortical excitatory neurons frequently collateralize and therefore may legitimately express more than one retrograde fluorophore. Our use of a winner-take-all (WTA) rule in the primary analyses was an intentionally conservative methodological choice designed to prioritize specificity over sensitivity in this proof-of-principle study.

As demonstrated in our simulations (Supp. Fig. 5–6), under realistic background and noise conditions, secondary assignments are more susceptible to false-positive errors than primary assignments. For this reason, we chose to assign a single primary identity for quantitative behavioral stratification while retaining additional above-threshold fluorophores as “secondary hits” and reporting their distribution separately (Supp. Fig. 7).

We did not intend to imply that projections are exclusive. Rather, the WTA strategy provides a conservative lower-bound estimate of subtype proportions and avoids inflation of dual-label rates under conditions where spectral separability is imperfect.

We agree that this rationale should be stated more explicitly in the manuscript, and that the potential impact of assignment strategy on subtype fractions and behavioral comparisons should be acknowledged clearly as a methodological trade-off rather than a biological claim.

Importantly, the biological analyses presented in this manuscript are illustrative demonstrations of functional stratification capability and do not depend on exclusivity of projection identity. We have revised the manuscript to clarify this framing as follows:

“If multiple fluorophores exceeded the threshold for an ROI, the fluorophore with the largest z-scored beta value was assigned as the primary identity (winner-take-all rule). This conservative approach was chosen to prioritize specificity under realistic noise and background conditions. Additional above-threshold fluorophores were retained as ‘secondary hits’ but were not incorporated into primary subtype stratification analyses.” (Methods, Single Pass Algorithm)

“For quantitative behavioral comparisons, each ROI was assigned a single primary fluorophore identity using a winner-take-all rule. We emphasize that this assignment strategy does not imply projection exclusivity. Rather, it provides a conservative lower-bound estimate of subtype proportions, as ROIs exceeding threshold for multiple fluorophores were classified according to their strongest spectral contribution.” (Result, Fluorophore distribution in behaviorally relevant ROIs)

“These analyses were performed using conservative single-label assignments; dual-threshold ROIs were not treated as co-identities in order to avoid overinterpretation of potentially ambiguous multi-label cells. Because identity assignment prioritizes specificity and classification uncertainty was not formally propagated into downstream comparisons, subtype fractions and behavior-by-subtype differences should be interpreted as qualitative demonstrations of projection-resolved functional stratification rather than precise anatomical quantifications. ” (Results, Neuronal Cell Type and Behavior)

“Cortical pyramidal neurons frequently collateralize to multiple downstream targets, and accordingly some ROIs exceeded threshold for more than one fluorophore. In this proof-of-principle implementation, we adopted a specificity-first winner-take-all assignment rule for primary analyses to minimize false-positive multi-label calls under realistic noise conditions. This strategy likely underestimates the true prevalence of dual-projecting neurons and should therefore be interpreted as a conservative stratification approach rather than a statement of projection exclusivity.” (Discussion)

(2) Dual-label detection is acknowledged but remains descriptive in vivo: the manuscript explicitly discusses the possibility of dual projection, evaluates dual-fluorophore detection in simulations (including performance under realistic noise/background), and reports in vivo rates of secondary hits. However, these dual-threshold events are not incorporated as co-identities in the main statistical analyses, making it difficult to judge how robust the principal biological conclusions are to the single-label decision rule.

We thank the reviewer for this important clarification request.

We agree that dual-projection neurons are biologically plausible and that dual-threshold ROIs were detected in vivo. In this manuscript, however, our primary goal was to establish the feasibility of high-dimensional spectral assignment and projection-resolved stratification, rather than to provide a definitive quantification of projection convergence.

For this proof-of-principle study, we chose a conservative winner-take-all (WTA) framework for primary behavioral analyses in order to minimize false-positive multi-label assignments under realistic noise and background conditions, as demonstrated in our simulations (Supp. Fig. 5–6). Secondary hits were retained and reported descriptively (Supp. Fig. 7), but not incorporated into the primary statistical comparisons to avoid overinterpretation of potentially ambiguous dual-label calls.

Importantly, the principal biological conclusions presented in the manuscript are qualitative demonstrations that projection-defined stratification is feasible within a single animal. These conclusions do not rely on projection exclusivity or on precise quantification of dual-projecting fractions.

We agree that this distinction should be made clearer in the manuscript, and we have revised the text as follows:

“Although dual-threshold ROIs were detected in vivo, these secondary assignments were not incorporated as co-identities in the primary behavioral analyses. This decision reflects a conservative specificity-first framework designed to minimize false-positive multi-label calls under realistic noise conditions. Accordingly, dual-label rates reported here should be interpreted descriptively. The present study focuses on demonstrating the feasibility of projection-resolved stratification, rather than providing definitive quantification of projection convergence.” (Results, Fluorophore distribution in behaviorally relevant ROIs)

“We then stratified these neurons by projection target and examined behaviorally selective activity across cell types. These analyses were performed using conservative single-label assignments; dual-threshold ROIs were not treated as co-identities in order to avoid overinterpretation of potentially ambiguous multi-label cells. Because identity assignment prioritizes specificity and classification uncertainty was not formally propagated into downstream comparisons, subtype fractions and behavior-by-subtype differences should be interpreted as qualitative demonstrations of projection-resolved functional stratification rather than precise anatomical quantifications.” (Results, Behavioral Analysis)

(3) Uncertainty is not propagated: False-positive/false-negative rates from simulations and uncertainty from registration/segmentation are not carried forward into quantitative confidence bounds on subtype proportions or behaviour-by-subtype effects.

We agree that formal propagation of classification and registration uncertainty into subtype proportions and behavioral comparisons would be appropriate in a study primarily focused on precise anatomical quantification. However, the central goal of the present manuscript is methodological and to demonstrate that high-dimensional spectral identity can be reliably linked to miniscope-recorded functional activity within a single animal.

We have shown that simulations under realistic noise, background, and class imbalance conditions (Supp. Fig 5-6) show that errors are predominantly false negatives rather than false positives. However, behavioral analyses are presented as qualitative demonstrations of the feasibility of projection-resolved stratification rather than as definitive quantitative anatomical measurements.

In the revised manuscript, we clarified that 1) subtype proportions and behavioral effects are assignment-dependent estimates, 2) simulation-derived error rates provide guidance for experimental design rather than formal confidence intervals, and 3) future studies centered on precise quantification of projection fractions would benefit from formal uncertainty modeling, as follows:

“These simulation-derived accuracy estimates characterize expected performance under defined noise and background conditions but were not formally propagated into confidence bounds on subtype proportions or behavioral comparisons. In this proof-of-principle study, subtype fractions are presented as assignment-dependent estimates rather than definitive anatomical measurements.” (Results, Assessment of spectral unmixing approach)

“Because classification uncertainty was not formally propagated into these analyses, behavior-by-subtype comparisons should be interpreted as qualitative demonstrations of functional stratification rather than precise quantitative estimates.” (Results, Neuronal cell types and behavior)

“The modeling framework was designed to characterize expected classification behavior across a range of experimental regimes, including background fluorescence, class imbalance, and reduced signal-to-noise ratio. These simulations provide practical performance guidance but were not used to compute formal error bars or propagate uncertainty into downstream biological analyses.” (Methods, Modeling of experimental variables to assess accuracy of algorithms)

“Because the present study is designed to establish methodological feasibility rather than precise anatomical quantification, simulation-derived false-positive and false-negative regimes were not formally propagated into confidence bounds on subtype proportions or behavioral effect sizes. Accordingly, subtype fractions should be interpreted as assignment-dependent estimates rather than definitive anatomical measurements. Future implementations could incorporate Bayesian or likelihood-based classifiers to generate posterior identity probabilities and enable formal uncertainty propagation when quantitative estimation of projection convergence is central to the biological question.” (Discussion)

Reviewer #3 (Public review):

This manuscript presents Neuroplex, a technically rigorous and carefully validated pipeline that links miniscope calcium imaging in freely behaving animals with high-dimensional fluorophore-based cell-type identification using in vivo multiplexed spectral confocal imaging through the same implanted GRIN lens. The work overcomes a major practical limitation of head-mounted microscopy by enabling the identification of up to nine projection-defined neuronal populations within the same animal, without post-fixation histology. The approach is well motivated and supported by extensive calibration and simulation. While the biological results are primarily illustrative, the methodological contribution is clear and likely to be broadly useful.

Major comments

(1) The approach relies on the assumption that fluorophore identity assigned during anesthetized confocal imaging accurately reflects the identity of neurons recorded during prior behavioural sessions. While the use of the same GRIN lens and in vivo co-registration mitigates many concerns, the manuscript would benefit from a more explicit discussion, or empirical demonstration, if available, of the stability of fluorophore assignments across time. Even limited repeat spectral imaging in a subset of animals would strengthen confidence in longitudinal applicability.

We thank the reviewer for highlighting this important conceptual assumption.

Fluorophore identity in Neuroplex is genetically encoded via AAVretro delivery and therefore does not depend on transient physiological state. Spectral imaging is performed in vivo through the same GRIN lens and field of view used during behavioral imaging, and co-registration relies on anatomical landmarks. While repeat spectral imaging was not formally performed as a longitudinal experiment, the underlying fluorescent protein expression is stable over weeks, and there is no biological mechanism in this paradigm that would alter fluorophore identity across sessions.

We revised the manuscript to explicitly state this assumption and clarify why identity stability is expected as follows:

“…fluorophore signals and reduce unmixing fidelity, leading to an increased false positive rate. Fluorophore identity in this framework is genetically encoded via retrograde AAV delivery and is therefore expected to remain stable across behavioral and spectral imaging sessions. Because both functional and spectral data are acquired in vivo through the same GRIN lens and co-registered using anatomical landmarks, assignment stability is not expected to vary across time unless expression levels change substantially. While repeat spectral imaging was not performed as a formal longitudinal experiment in this study, the stability of fluorescent protein expression supports the assumption that fluorophore identity reflects a persistent cellular attribute.” (Discussion)

(2) Fluorophore identity is determined using thresholding of linear unmixing coefficients relative to an empirically defined baseline, followed by a second adaptive pass for over-represented fluorophores. While this heuristic is extensively validated via simulations, it remains ad hoc from a statistical perspective. The authors should more explicitly justify this choice and discuss its limitations relative to probabilistic or likelihood-based classifiers, particularly with respect to uncertainty estimation at the single-ROI level.

We agree that the dual-pass thresholding approach is heuristic rather than fully probabilistic. More formal probabilistic classifiers are possible but would introduce additional modeling assumptions and training requirements beyond the scope of this proof-of-principle study.

We revised our manuscript to clarify this as follows:

“The current classification framework relies on linear unmixing followed by empirically defined thresholding rather than full probabilistic inference. This approach provides transparency and practical robustness under realistic noise and background conditions but does not generate single-ROI posterior uncertainty estimates. ” (Discussion)

(3) Identifiability of fluorophores is demonstrated empirically, but the manuscript does not explicitly quantify spectral separability (e.g., similarity metrics between basis spectra or conditioning of the unmixing matrix). A brief analysis of spectral independence or sensitivity of beta estimates to noise would provide mathematical reassurance, especially given the reliance on linear regression in a high-dimensional feature space.

We agree that spectral separability is conceptually important. In this manuscript, separability is demonstrated empirically through 1) In vitro fingerprint acquisition under identical optical conditions, 2) simulation under background and noise, and 3) successful in vivo classification across regimes. We did not compute formal matrix conditioning metrics, but we agree that the separability rationale should be described more explicitly. We revised our manuscript as:

“While formal conditioning metrics were not explicitly computed empirical fingerprint acquisition and simulation-based perturbation analyses demonstrate sufficient spectral independence for reliable linear unmixing under the tested regimes.” (Discussion)

(4) The spectral unmixing treats CNMF-derived ROIs as fixed supports. I wonder whether ROI boundaries, neuropil contamination, and partial overlap can introduce structured uncertainty that could bias spectral estimates. If so, the authors should acknowledge this dependency more explicitly and discuss how ROI quality or overlap might influence false negatives or false positives, particularly in densely labelled regions.

We agree that ROI definition influences spectral extraction. Spectral fingerprints are derived by averaging all pixels within the ROI mask, and therefore neuropil contamination, partial ROI overlap, and dense labeling could influence beta estimates. In the revised manuscript, we have acknowledged this dependencies more explicitly.

“Spectral unmixing operates on CNMF-derived ROI masks treated as fixed supports. Accordingly, segmentation quality, neuropil contamination, and partial overlap between neighboring cells can influence extracted spectral fingerprints and may contribute to false negatives or secondary assignments, particularly in densely labeled regions. These structured sources of uncertainty are expected to have the greatest impact under regimes of extreme class imbalance, low fluorophore brightness, strong neuropil signal, or pairing of spectrally overlapping reporters. Use of refined segmentation strategies or nuclear-localized reporters could reduce such structured uncertainty in future implementations.” (Discussion)

(5) The manuscript reports meaningful rates of secondary fluorophore detection, but also nontrivial false-positive rates for secondary labels under realistic conditions. The authors appropriately caution against over-interpretation, but the Discussion should more clearly delineate when dual-label assignments are likely to be biologically interpretable versus methodologically ambiguous, and how experimental design (e.g., fluorophore pairing) should be optimized accordingly.

We agree and will delineate interpretability boundaries explicitly.

“Dual-label assignments are most reliable when fluorophores are spectrally well separated and when signal-to-noise ratios are high. In contrast, spectrally adjacent fluorophore pairs or densely labeled regimes increase ambiguity and false-positive risk. Experimental design should therefore prioritize pairing spectrally distant fluorophores when projection convergence is of primary interest.” (Discussion)

(6) I suspect that Neuroplex will be most effective in certain regimes (moderate convergence, bright and spectrally distinct fluorophores) and less reliable in others. A more explicit discussion of best practices, anticipated failure modes, and experimental scenarios where the method may be inappropriate would increase the practical value of the paper for adopters.

“More broadly, Neuroplex is expected to perform most robustly in regimes characterized by moderate projection convergence, balanced fluorophore representation, bright and spectrally distinct reporters, and adequate signal-to-noise ratio. Imaging directly within a projection target that has received dense retrograde labeling may introduce substantial class imbalance, which simulations predict will reduce detection sensitivity for the dominant fluorophore. In such cases, conservative assignment strategies, reduced spectral complexity, or refinement of ROI definition may improve interpretability. Careful fluorophore selection and pilot validation under intended imaging conditions are therefore recommended prior to large-scale application. Future implementations incorporating nuclear-localized reporters may further reduce segmentation-dependent ambiguity by constraining spectral signals to somatic compartments.”

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The authors should address a few points that are not clear.

(1) At the end of the Results, the authors assess their approach using only four fluorophores and conclude that Neuroplex works "even" under reduced complexity. There is something I am missing. In my mind, lower complexity should be easier and should work better. As a researcher, I would first assess a four-fluorophores scenario and then step up with complexity, but the authors did the opposite. Also, I think that the present Supplementary Figure 9 should be in the main text; I don't understand why the authors decided to relegate a clear result to the bottom of everything. The authors should give some explanations.

We agree that reduced spectral complexity should, in principle, improve separability and classification performance. Our original presentation order was intended to first demonstrate feasibility under the most challenging condition (nine fluorophores plus GCaMP), thereby establishing maximal multiplexing capacity. The reduced-complexity experiment was included to demonstrate scalability and generalizability under more typical experimental regimes. However, we agree that this rationale was not sufficiently clear and that the reduced-complexity results merit presentation in the main text.

Accordingly:

We have moved former Supplementary Figure 9 into the main Results (Fig. 6).

We have clarified explicitly why the nine-fluorophore condition was presented first as follows:

“To evaluate the performance of Neuroplex under more typical experimental regimes with reduced-complexity, we applied the pipeline to two GCaMP transgenic animals injected with a subset of four fluorophores.”

(2) The question of relative expression is crucial. Among the infected regions, there is the contralateral mPFC and I imagine that if they image there, the contribution of the expressed protein might dominate all other components, preventing detection of other fluorophores, including GCaMP. But is it the case, or would it be possible to detect projecting neurons in that region? I would be surprised that the authors never tried it; this test would simply imply mounting the GRID lens on the other hemisphere.

This is an important conceptual point.

Our simulations (Supp. Fig. 5) explicitly model over-representation of a single fluorophore. These results show that heavy class imbalance primarily increases false negatives (due to baseline normalization) rather than false positives.

In the revised manuiscript, we discussed this limitation more explicitly.

“Relative fluorophore representation within the imaged field of view influences classification robustness. As demonstrated in our simulations of class imbalance (Supp. Fig. 5g–h), extreme over-representation of a single fluorophore primarily increases false-negative rates due to baseline normalization effects. In the present study, we intentionally avoided imaging directly within heavily infected projection targets (e.g., contralateral mPFC) in order to maintain moderate fluorophore representation across ROIs. Imaging in a densely labeled region would represent a more challenging regime, and we would expect reduced sensitivity for the dominant fluorophore under such conditions.” (Dicussion)

(3) The possibility to utilise Neuroplex goes beyond the type of experiment presented as proof-of-concept in this technical paper. In the Discussion, the authors mention genetically defined subtypes and activity-tagged neurons. But, if one changes the pipeline, can it be used by expressing GECIs with different spectra, or GECIs and genetically-encoded voltage indicators (GEVIs)? I would be very interested in knowing what the authors think about this putative "shortcut".

We thank the reviewer for this forward-looking and insightful question.

In principle, the Neuroplex framework could be extended to incorporate spectrally distinct genetically encoded functional indicators, including multi-color GECIs or combinations of GECIs and GEVIs. However, it is important to distinguish this from the identity-assignment strategy implemented in the present study.

Simultaneous multi-color functional imaging under a head-mounted miniscope is optically more demanding than assigning cell identity from single-color functional recordings followed by high-dimensional spectral readout. Multi-color GECI or GEVI imaging requires real-time excitation and emission separation during dynamic recording, increases optical complexity, and is particularly sensitive to chromatic aberration, photon efficiency, and signal-to-noise constraints imposed by GRIN lenses.

In contrast, Neuroplex decouples functional acquisition from spectral identity determination. Functional activity is recorded using a single optimized channel, while spectral separation is performed separately under controlled confocal conditions with multiplexed excitation and emission sampling. This design substantially reduces optical burden during behavioral imaging.

While integration of multiple functional reporters is conceptually feasible within this framework, successful implementation would require careful validation of brightness, spectral separability, and temporal stability for each reporter combination.

Reviewer #2 (Recommendations for the authors):

(1) Implement a principled multi-label calling mode for cells with >1 above-threshold fluorophore (e.g., per-fluorophore FDR control or Bayesian posteriors). Report cell-wise weights and re-run key results three ways: single-label, hard multi-label, and soft (probabilistic) assignments; state explicitly how conclusions change.

We appreciate this suggestion and agree that multi-label or probabilistic calling frameworks are well motivated, particularly for studies in which projection convergence is the central biological question. In the current manuscript, however, our goal is to establish a practically deployable proof-of-principle pipeline for linking miniscope functional recordings to a high-dimensional spectral-identity readout. Consistent with this scope, we used a conservative winner-take-all (WTA) strategy for primary analyses to prioritize specificity under realistic noise and background conditions, and we treated multi-hit events descriptively. Importantly, the qualitative conclusions regarding projection-resolved functional stratification are unchanged when secondary-hit distributions are examined.

In the revised manuscript, we explicitly stated that: (i) single-label assignment is a conservative analysis choice rather than a biological claim of exclusivity, and (ii) multi-label or probabilistic calling is a natural extension for future work, as follows:

“If multiple fluorophores exceeded the threshold for an ROI, the fluorophore with the largest z-scored beta value was assigned as the primary identity (winner-take-all rule). This conservative approach was chosen to prioritize specificity under realistic noise and background conditions. Additional above-threshold fluorophores were retained as ‘secondary hits’ but were not incorporated into primary subtype stratification analyses.” (Methods, Single Pass Algorithm)

“Because the present study is designed to establish methodological feasibility rather than precise anatomical quantification, simulation-derived false-positive and false-negative regimes were not formally propagated into confidence bounds on subtype proportions or behavioral effect sizes. Accordingly, subtype fractions should be interpreted as assignment-dependent estimates rather than definitive anatomical measurements. Future implementations could incorporate Bayesian or likelihood-based classifiers to generate posterior identity probabilities and enable formal uncertainty propagation when quantitative estimation of projection convergence is central to the biological question.” (Discussion)

(2) Add ground truth for dual projectors in a subset (paired orthogonal tracers or staged injections) and provide a confusion matrix including dual-positives; use this to calibrate thresholds/priors.

We agree that ground truth validation of dual projectors using orthogonal tracers or staged injections would be valuable, particularly for calibrating priors and enabling confusion-matrix-based evaluation. However, these experiments require additional cohorts and experimental design beyond the scope of the current proof-of-principle technical manuscript. Our goal here is to demonstrate the feasibility of multiplexed identification and projection-resolved stratification within a single animal, not to provide definitive anatomical quantification of collateralization.

We have revised the manuscript to clearly state that dual-label in vivo observations are descriptive and that studies aimed at quantitative convergence mapping should incorporate orthogonal ground truth validation.

“Accurate quantification of projection convergence would benefit from orthogonal ground-truth validation (e.g., paired tracers or staged injections) to establish confusion matrices for dual positives and to calibrate thresholds or priors.”

(3) Propagate uncertainty from simulations and registration/segmentation to subtype fractions and behavior effects (error bars or sensitivity analyses).

We agree that formal uncertainty propagation is appropriate for studies focused on precisely quantifying subtype proportions or effect sizes. In this manuscript, subtype fractions and behavioral comparisons are presented primarily as demonstrations of the feasibility of projection-resolved functional stratification, rather than definitive anatomical measurements. Simulation analyses are included to characterize expected performance under defined noise and background regimes, but we did not propagate these uncertainties into downstream confidence bounds in this proof-of-principle work.

We have revised the manuscript to clarify this explicitly as follows:

“These simulation-derived accuracy estimates characterize expected performance under defined noise and background conditions but were not formally propagated into confidence bounds on subtype proportions or behavioral comparisons. In this proof-of-principle study, subtype fractions are presented as assignment-dependent estimates rather than definitive anatomical measurements.” (Results, Assessment of spectral unmixing approach)

“These analyses were performed using conservative single-label assignments; dual-threshold ROIs were not treated as co-identities in order to avoid overinterpretation of potentially ambiguous multi-label cells. Because identity assignment prioritizes specificity and classification uncertainty was not formally propagated into downstream comparisons, subtype fractions and behavior-by-subtype differences should be interpreted as qualitative demonstrations of projection-resolved functional stratification rather than precise anatomical quantifications.” (Results, Neuronal cell types and behavior)

“The modeling framework was designed to characterize expected classification behavior across a range of experimental regimes, including background fluorescence, class imbalance, and reduced signal-to-noise ratio. These simulations provide practical performance guidance but were not used to compute formal error bars or propagate uncertainty into downstream biological analyses.” (Methods, Modeling of experimental variables to assess accuracy of algorithms)

“Because the present study is designed to establish methodological feasibility rather than precise anatomical quantification, simulation-derived false-positive and false-negative regimes were not formally propagated into confidence bounds on subtype proportions or behavioral effect sizes. Accordingly, subtype fractions should be interpreted as assignment-dependent estimates rather than definitive anatomical measurements. Future implementations could incorporate Bayesian or likelihood-based classifiers to generate posterior identity probabilities and enable formal uncertainty propagation when quantitative estimation of projection convergence is central to the biological question.” (Discussion)

(4) Mitigate sources of spurious multi-hits (neuropil handling, ROI mask erosion, nuclear-localized reporters, spectral basis choices) and quantify their impact on dual-label recovery.

We agree that neuropil contamination, ROI boundary choices, and spectral basis selection can influence multi-hit rates. In the current manuscript, we already implement background subtraction and evaluate multi-hit behavior through simulations under realistic background and noise regimes. Quantitative evaluation of additional mitigation strategies (e.g., ROI erosion comparisons) would require new analyses beyond the current scope.

We have revised the Discussion to include concrete best-practice recommendations (e.g., fluorophore pairing, conservative interpretation of multi-hits, and potential use of nuclear-localized reporters).

“Multi-hit events can reflect true biological collateralization but may also arise from structured sources of ambiguity such as neuropil contamination, partial ROI overlap, or imperfect ROI boundaries. These factors may bias spectral estimates and contribute to secondary assignments, particularly in densely labeled regions. Practical mitigation strategies include conservative assignment rules, improved segmentation, and use of nuclear-localized reporters to reduce neuropil contribution. ”

(5) Clarify claims in the main text/figures wherever exclusivity is implied; label which panels use single-label vs multi-label/soft assignments.

We agree and thank the reviewer for emphasizing clarity. We did not intend to imply projection exclusivity. We have revised the manuscript text and figure legends to explicitly state where single-label (winner-take-all) assignment is used, and to avoid language that could be read as claiming exclusive projection identity as follows:

“For quantitative behavioral comparisons, each ROI was assigned a single primary fluorophore identity using conservative winner-take-all rule. This assignment reflects the strongest spectral contribution and does not imply projection exclusivity. Rather, it provides a conservative lower-bound estimate of subtype proportions, as ROIs exceeding threshold for multiple fluorophores were classified according to their strongest spectral contribution.”

Reviewer #3 (Public review):

Summary:

This important work provides a web-based tool to contextualize effect sizes in psychiatry with respect to reliability and base rates (collectively referred to as predictive utility analysis). The methods for the tool incorporate established psychometric principles that I think are of use for multiple fields in this seemingly easy-to-use tool. I agree with the critical importance of this tool and the methodological points made in this manuscript. Enthusiasm for the manuscript is weakened by a lack of clarity on the formulation of the paper and stated goals of the examples used, with the inferences and impact on clinical decision making from various parameterizations via this tool left open-ended.

Strengths:

This paper presents a well-considered and, what I think will be highly useful, web-based tool to contextualize effect sizes with respect to reliability and base rates. As the authors rightly point out, such a tool could be used in conjunction with widespread analytic power analysis tools in study planning. The paper also well contexualizes the need for such a tool in the relatively recent history of concerns of power, reliability, and inference in psychiatry specifically, and more general meta-scientific debates in psychology and neuroscience.

Weaknesses:

My primary feedback on this manuscript is the lack of clarity in what the paper itself, specifically, separate from the tool, is hoping to achieve. There is a central, but unresolved, tension in whether the reader is supposed to:

(1) focus on the specifics of the examples used and whether to reevaluate the substantive claims from the studies, (2) buy in to how various reliability and base rate parameters impact modeling outcomes, (3) receive an introduction to the tool itself.

In my estimation, the largest contribution to the field here is in (2) and (3), but currently much of the real estate of the paper is dedicated to several examples of (1). While these specific examples may be illustrative to some degree, I think given the number and brevity of such, they are unlikely to incidentally achieve points (2) and (3) above. Specific examples include the assertion of kappas for DSM diagnoses, without much nuance (e.g., see https://psycnet.apa.org/buy/2015-27500-001). Given the relatively limited space given to this example, however, it's hard to be entirely certain what the reviewer should take away.

A second point of concern is where this tool would be situated in the research pipeline. I agree with the authors that this tool could be used in ways that parallel power analysis. With that in mind, it seems the most common use of this tool for an individual investigator is likely to be in a priori study planning. In contrast, and with my point above in mind, the use of the tool for existing results is likely best done with multiple estimates of effect sizes, reliability, and base rates, as is common in meta-analysis or consensus reviews. Nevertheless, there is no real example or guidance around how this influences new study planning.

A third point is that more nuance would be useful in the introduction about the current state of psychiatry research. For example, I share many of the authors' concerns about reliability, power, reproducibility, and barriers to translation. That said, it is the case that while effect sizes should be considered considerably more, they are widely considered in psychiatry research via the common place of meta-analysis and other data pooling approaches. Another such example that the authors state in the context of reliability: "However, this [reliability] attenuation is rarely accounted for in routine analyses in psychiatry". This is true in practice, but somewhat misleading insofar as the method by which to do this remains unclear. For example, should we all report disattenuated associations, assuming there is no error and everything is perfectly reliable? This, of course, would be unrealistic to expect zero error. That we can achieve this with the new tool is clear, but the nuance of how and under what circumstances it should be done is not clear, and such nuance should be better reflected in the framing of the problem. That is, there is also a lack of clarity on what ought to be best practices and field-wide goals, rather than simply the lack of an ability to model these factors.

Minor point

For conceptual clarity, it would benefit the manuscript to at least briefly mention the role of validity in translational importance. Of course, the current psychometric issues of reliability, base rate, power, etc are critical, but it should at least be mentioned, given the potential wide audience of this manuscript, validity is important as well. For example, highly reliable measures may not be valid indicators of underlying disease etiology (e.g., fMRI head motion is a highly reliable trait-level feature, but typically not considered an important predictor or consequence of mental health worth investing translational resources in). Relatedly, confounding as a general topic would be useful to mention just briefly, to help with the spirit of considering underlying issues in translation.

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Reply to the reviewers

Reviewer #1 (Evidence, reproducibility, and clarity (Required)):

Summary: In this manuscript, the authors examine how peripherin-2 (PRPH2) contributes to the localization of CNGβ1 within rod outer segment structures. PRPH2 and its homolog ROM1 are structural components of rod discs and are required for disc morphogenesis. In the absence of PRPH2, rod outer segments do not form, and various outer segment materials accumulate and are released as cilia-derived ectosomes. PRPH2 is thought to be transported through an unconventional secretory pathway, whereas cGMP-gated channels follow a conventional trafficking route. Although these components reach the outer segment through distinct pathways, PRPH2 is necessary for the proper delivery of CNGB1, a subunit of the cGMP-gated channel, to its correct destination. It was previously reported that a small fraction of PRPH2 reaches the outer segments through the conventional pathway when it forms a complex with Rom1 in mouse photoreceptors. Using Rom1 KO mice, the authors show that this conventionally trafficked PRPH2 fraction is not required for CNGB1 transport to the outer segment. Using various chimeric constructs, the authors verified that tetraspanin core of PRPH2, delivered to the OS, is sufficient to promote OS localization of CNGB1. Ct and Nt cytoplasmic regions of PRPH2 are dispensable for the role. Overall, the majority of the experiments are well-executed with statistical rigor, written in a way that others can reproduce, and support the major conclusion indicated in the title, "PRPH2 is essential for OS localization of CNGB1".

Major comments: I believe that the majority of the conclusions are well-supported in this manuscript. Below, I am listing the major points that may need additional experiments or clarifications: 1) CNGA1 subunit is transported to and enriched within ciliary exosomes or the outer segment in PRPH2 deficient mice (Figure 1). The reduced levels of CNGA1 and CNGB1 in rds-/- mice suggest limited stability of these proteins. Their diminished abundance is also influenced by decreased mRNA expression of the corresponding genes. These findings imply that CNGB1 may not be essential for outer segment delivery of cGMP-gated channels if CNGA1 alone contains adequate targeting information. Related to these points, it is unclear whether CNGB1 exhibits a trafficking defect or encounters other problems before leaving the endoplasmic reticulum. Such problems may involve deficiencies in folding, holo-channel assembly, or related quality control processes.

RESPONSE: We agree with this reviewer and have added additional data and interpretation to address this point. Our new data finds that in fact a low level of CNGB1 can reach ectosomes in rds-/- rods, which makes sense since we and others had observed CNGA1 was present and we know that channel assembly occurs in the ER. This suggests that the CNG channel can properly fold and assemble. Furthermore, overexpressing CNGB1 did not restore ciliary localization in Rds-/-, leading to our interpretation that in the absence of an outer segment membrane compartment, there is no place to deliver the CNG channel and it is subsequently degraded. Apart from perihperin’s binding partner, ROM1, this is unique to the CNG channel. CNG channel subunits are still significantly lower at P21 than other outer segment membrane proteins, such as ABCA4 (shown here), rhodopsin, and PCDH21(shown elsewhere).

2) CNGB1 overexpression in rds-/- mice does not result in outer segment localization of CNGB1 channels (Figure 2A). These findings do not clarify whether CNGB1 successfully transits through the Golgi apparatus or associates properly with CNGA1 subunits. Elevating expression levels alone would not compensate for problems in folding or assembly.

RESPONSE: We recognize that our previous submission lacked clarity on this point. Therefore, we have restructured the order of figures and provided additional controls to improve our manuscript. First, the fact that CNG channel is present at P21 and even increases over time suggests that in rds-/- rods channel processing (folding and assembly) is unaffected. Second, we recognize that channel stoichiometry is important for proper channel assembly, so we added a new supplementary figure that shows endogenous CNGA1 expression increases in rds-/- rods that are overexpressing myc-CNGB1 and FLAG-peripherin-2. This adds credence to our CNGB1 overexpression experiments and shows that CNGB1 being trapped is not due to inefficient channel assembly.

3) Claims related to Figure 6 (P45 rds-/-) need further evidence. It remains uncertain whether CNGA1 and CNGB1 are delivered to lamellar ciliary membranes or to a distinct plasma membrane compartment comparable to that observed in wild type rod outer segments, or whether they accumulate in ciliary ectosomes. Those lamellar structures could be a part of cone outer segments. The observed GARP signal may originate solely from soluble GARP proteins. It is also unclear if CNGA1 and ROM1 colocalize in P45 rds-/- mice. Clarifying these points would strengthen the conclusion that lamellar formation, rather than specific function of PRPH2, is sufficient for CNGB1 delivery to the cilium or outer segment plasma membrane.

RESPONSE: CNGA1/B1 are not expressed in cones, so the elevated outer segment localization observed at P45 must be coming from rods. In mouse retina, cones make up only 3% of the photoreceptor population. The SEM data clearly show that the lamellar ciliary protrusions are present on the majority of the photoreceptors. We now include CNGB1 staining from Rds-/- P45 sections that corroborate these data and show that CNGB1 is present at P45 and not P21 (Supplemental Figure 2).

Below are minor comments: 1) The study does not establish whether a direct interaction between PRPH2 and CNGB1 is required for CNGB1 delivery to rod outer segments. Prior work by the senior author (ref 13) suggests that this interaction is not essential, since the PRPH2 binding site within the GARP domain is distinct from outer segment transport signal of CNGB1. Including a discussion of the PRPH2-GARP (or CNGB1) interaction and its relevance to CNGB1 trafficking would help readers interpret the findings more fully.

RESPONSE: We have included this in our discussion.

2) The authors propose that the ROM1 core is sufficient for outer segment delivery of CNGB1 based on experiments with chimeric constructs. However, in Figure 1, ROM1 is present in the outer segments (or ciliary ectosomes) of rds-/- mice even though CNGB1 is not delivered to these structures.

RESPONSE: Our new data, including MS analysis and Western analysis from an enriched ectosome preparation, reveal that, along with ROM1, low levels of the CNG channel are delivered to ciliary ectosomes in Rds-/- mice. However, at this early timepoint photoreceptor cilia do not produce a membrane protrusion, which we observe is required to augment CNG delivery. We expressed a FLAG-ROM1 construct to try to drive earlier creation of these membrane protrusions, but this was unsuccessful, as we observed ROM1 was primarily localized to the inner segment. This suggests that overexpression of ROM1 did not increase ROM1 delivery to the cilia. Luckily, we were able to overcome this bottleneck with several of our chimeric ROM1/Prph2 constructs that did localize to the cilia and restore CNG localization. All of these new results have been included in the revised manuscript.

3) Line 80: "Theouter" A space shall be inserted between "The" and "outer".

RESPONSE: Done

**Referee cross-commenting**

Both reviewer #2 and reviewer #3 express views that align with mine. They clearly described the study's limitations, and their comments are highly valuable.

Reviewer #1 (Significance (Required)):

Prior studies showed that CNGB1 is not present in cilia-derived ectosomes of rds-/- mice, indicating that PRPH2 is necessary for ciliary or outer segment localization of CNGB1 in rods. Building on these earlier findings, I consider this study significant for the following reasons: 1) Using detailed analysis of different PRPH2 domains and chimeric constructs, it clarifies that PRPH2 core region, delivered to OSs, is essential and sufficient for OS localization of CNGB1. 2) PRPH2 and CNGB1 are thought to travel through different post-ER transport routes, with one pathway bypassing Golgi regions and the other passing through them. This study shows that CNGB1 depends on PRPH2, which suggests that these two routes may converge or interact at later stages and opens new directions for future investigation. 3) The study is relevant to basic scientists and biologists investigating how membrane structures acquire specialized functions in neurons, and its implications extend beyond photoreceptor biology.

Limitation of the study: I believe that clarifying these points will make the manuscript more significant. 1) Is it not clear, as mentioned above, how PRPH2 contributes to the delivery of CNGB1 to the OSs in the different secretory pathways.

RESPONSE: In the absence of ROM1, Prph2 only travels through the unconventional secretory pathway directly from the ER. By looking at CNG trafficking and localization in ROM1-/- mice, we rule out the possibility that the small portion of PRPH2/ROM1 complexes that traffic conventionally through the Golgi are required for channel localization (Figure 3). Further, our Rho-Prph2 chimera that includes the trafficking signal from Prprh2 did not rescue CNGB1 localization (Figure 4). These findings suggest that it is unlikely that these proteins engage during secretory transport to the outer segment.

2) The prior study using a fluorescence complementation approach (Ritter et al, 2011) suggests that PRPH2 and CNGB1 can associate within rod ISs, likely before their delivery to OSs. However, it remains unclear whether this interaction supports the potential cotransport of CNGB1 and PRPH2 or whether the authors view these proteins as being transported independently.

RESPONSE: As described above, our experiments rule out the notion that co-transport through the Golgi is driving CNG channel ciliary localization. We now note in our discussion that this data does not rule out the possibility of an earlier association between these proteins. However, the bulk of our data supports that any early interaction is not required for ciliary delivery.

3) At the end of the result section (Figure 6, rds-/- P45), the authors suggest that lamellar formation (evaginations?) is required for CNGB1 transport. However, CNGB1 is normally not seen in evaginations or lamellar structures, and thus the assumption is not consistent with prior findings.

RESPONSE: Absolutely, we agree that the CNG channel does not enter newly forming disc membranes, which has been shown by multiple groups. We included this in our discussion and have now added a clearer statement of our hypothesis: “Together, these data suggest that the partitioning of disc membranes from the plasma membrane by tetraspanin proteins is a key step for localizing the CNG channel and could play a role in segregating other proteins into the plasma membrane.”

Overall, the manuscript is insightful and has the potential to advance our field and related disciplines.

RESPONSE: Thanks!

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

Cyclic nucleotide gated channels (CNG) localize to the plasma membrane of the rod photoreceptor outer segments, and are a key component of the phototransduction cascade. Understanding how outer segment proteins are trafficked and sequestered to the outer segments is an important field of investigation as it addresses both a fundamental aspect of cell biology and mechanism of disease, many of which have trafficking defects at the core of the pathogenic process. Using primarily IHC analysis of rodent models in combination with introduction of various expression constructs to the retina (through electroporation), this study finds that two rod outer segment structural proteins, peripheral-2 and ROM1, facilitate CNG channel localization to the outer segment.

While this conclusion is interesting, a major concern that tempers enthusiasm is that in peripherin-2 null photoreceptors, there are no outer bona fide segments. In lieu of outer segments, there are rudimentary membranous protrusions and vesicles distal to the connecting cilia where outer segments should be. So the basis for concluding that peripherin-2 is required for CNG localization to the outer segment seems a bit wobbly. It is understood that the authors assumed the membranous materials distal to cilia as proxy for outer segments in their analysis and narrative. This assumption may have some merits. However, it is well known that when outer segment morphogenesis is severely compromised, all normally outer segment-bound proteins are ectopically localized or largely absent due to increased degradation. This could be simply due to the loss of their destination compartment, among other things. It is not clear how the authors could distinguish between a direct causal relationship where loss of one protein leads to the mislocalization of another, from secondary outcomes due to loss of the outer segments. The last sentence of the Abstract is telling. "Interestingly, this notion is supported by endogenous staining of CNGB1, which reappears in aged Rds-/- rods that have produced ciliary membrane protrusions." So in aged mice CNGB1 did localize to the OS, but what changed? There was more OS like material to house the CNGB1 protein in the aged mice.

RESPONSE: We agree that the loss of the OS compartment is likely driving downregulation of all OS proteins and have included a statement as such in our manuscript. We also performed additional qRT-PCR analysis on ROM1 and ABCA4 to show global downregulation at the mRNA level – consistent with the notion that there are reduced outer segment proteins when morphogenesis is compromised. However, our Westerns and IHC (as well as published data) clearly find a specific decrease in the CNG channel at the protein level, suggesting that not all proteins behave similarly when the outer segment is not formed. We included additional discussion on this point as well. While not directly examined in our manuscript, previous reports have shown the reverse effect: some outer segment proteins (e.g. PCDH21, Prom1) are upregulated in rds-/- retinas (Rattner et al JBC 2004). Therefore, it is an oversimplification to state that all outer segment proteins behave the same when outer segments are not formed properly. Other models of outer segment dysmorphia (e.g. RhoKO, PCDH21KO, Prom1KO, or WASF3) localize the CNG channel properly. We have added this to the discussion and hope that by restructuring our manuscript, we clearly outline that we do think that membrane retention at the tip of the cilia is driving CNG channel localization and that molecularly the tetraspanin proteins play a role in organizing these membranes.

Reviewer #2 (Significance (Required)):

Trafficking of nascent proteins to the outer segment in support of its renewal is an important subject, which has significant impact in understanding the mechanisms of retinal degeneration. The conclusion from this study, that peripherin-2 and ROM1 have a direct role in supporting CNG subunit trafficking may well be meritorious. However the data presented are less than fully convincing, and specifically the question of a direct vs secondary effect needs to be better addressed.

RESPONSE: We appreciate this reviewer’s enthusiasm for investigating this process. The initial premise of our study was to investigate whether a direct effect of peripherin-2 on CNG delivery was possible, which was meritorious based on previously published data. However, we now find no direct trafficking link between CNG and peripherin-2; instead, our data largely find that CNG delivery is dependent on the presence of retained membranes at the ciliary tip – either through natural mechanisms or by driving “rudimentary” outer segment membrane lamination by overexpression of tetraspanin domains. We have restructured the manuscript to help guide the discussion.

The following quote underpins some of the reasoning in the study. Lines 139-144, "(Figure 2A). This localization pattern suggests that the CNGB1 subunit is trapped in the biosynthetic pathway. In contrast, when FLAG-tagged rhodopsin is overexpressed in Rds-/- rods it traffics properly to outer segment ectosomes (Figure 2B, (19)). We posit that without proper exit from the biosynthetic pathway, the endogenous CNGB1 protein is rapidly degraded to undetectable levels, which we circumvent through overexpression. These data suggest the localization defect of CNGB1 in Rds-/- rods is in the trafficking of CNGB1. " This in my view is an over- interpretation of limited data. The statement implies that rhodopsin and CNGB1 qualitatively differ in their fate but I would argue that both proteins are heavily degraded intracellularly except more of rhodopsin escaped to the "OS" and shows up in IHC. In many rhodopsin mutant transgenic mice, mutant rhodopsin appeared in OS even though intracellular degradation (gumming up the system) is a major factor in the disease process. The claim "rhodopsin trafficked properly to outer segment ectosomes" is not grounded in solid data.

RESPONSE: We do fundamentally agree that the endogenous CNG channel is heavily degraded, which we confirm by overexpressing an exogenous CNGB1-myc and finding it trapped in the biosynthetic pathway. As stated by the reviewer, this localization pattern is in contrast to what we and others have observed for endogenous rhodopsin, and now show for overexpressed FLAG-rhodopsin – that rhodopsin does traffic to the OS ectosomes. By comparing the localization of both endogenous and overexpressed constructs (using the same promoter), we feel that our conclusion is well supported. We appreciate that our wording of “rhodopsin trafficked properly to the outer segment” is misleading, as traffic of membrane proteins in Rds-/- rods is generally affected and not “proper”. Importantly, we follow up this “limited data” with additional experiments showing that at high expression levels, we are unable to drive CNGB1 localization to OS ectosomes unless we co-express with a tetraspanin domain.

A further minor comment is that the scope of the study appear limited, with no attempted experiments on how these proteins might interact to effect facilitation of trafficking.

RESPONSE: Our approach was to be agnostic to the outcome of our hypothesis that peripherin-2 was directly involved in CNG channel trafficking. The experiments we performed to test this (ROM1-/- analysis and Prph2 C-terminal chimeras) did not support a role for peripherin-2 in CNG trafficking. Instead, our data support a model in which membrane retention and organization at the ciliary tip drives CNG channel delivery. We feel that our approach was not limited.

Reviewer #3 (Evidence, reproducibility and clarity (Required)):

in the gene encoding tetraspanin protein peripherin 2 (Prph2), i.e., Rds-/-, examining the requirements for various portions of the Prph2 protein in the context of an assortment of chimeric constructs expressed via transfection into photoreceptor cells, to restore localization of the beta subunit of the cyclic nucleotide-gated channel (CNGbeta1) to photoreceptor outer segments (OS) (in a small number of experiments) or, in the majority of experiments, to do so for a recombinant tagged version of this protein also overexpressed by transfection.

The concluding sentences of the Discussion, which summarize the major conclusions are as follows: "Our data clearly show that localization of the CNG channel is dependent upon peripherin-2 after biosynthetic exit, further suggesting that the necessary action is at the ciliary base. Supporting evidence for this comes from analysis of Rhodopsin knockout outer segments which have internal disc-like structures and localize CNG channel properly. Therefore, in the absence of a fully elaborated outer segment, peripherin-2's ability to delineate a disc is sufficient to drive CNG channel delivery. Together, these data suggest that the partitioning of disc membranes from the plasma membrane by tetraspanin proteins is a key step for trafficking the CNG channel and could play a role in segregating other proteins into the plasma membrane.

The first sentence contains both reasonable conclusions and phrases whose meaning is unclear or not supported by the results presented. The statement: 'localization of the CNG channel is dependent upon peripherin-2 is supported by the data but, of course, has long been known from previous studies of Rds-/- mice. What is meant by "...after biosynthetic exit..." is unclear. If, by this term, apparently newly invented, the authors mean "after its synthesis of the protein is complete," the statement is accurate, but also a truism.

RESPONSE: The absence of CNGB1 was reported in previous studies, but the mechanism driving its absence has not been investigated. In our resubmission, we have added additional data that now shows CNGB1 is present at very low levels in Rds-/- ectosomes but remains undetectable by IHC, which is consistent with previous studies mentioned by the reviewer, but is also a novel finding. Importantly, we find specific downregulation of CNG channel subunits in Rds-/- retinas compared to ABCA4, supported by Western blot analysis (Figure 1), and we investigate the mechanism driving this result.

We appreciate the reviewer pointing out that “biosynthetic exit” is a niche term not broadly understood. We have removed this statement.

The statement, "the necessary action is at the ciliary base," is NOT supported by the data presented, as the effect of the "successful" Prph2 constructs on CNGbeta1 localization is primarily to increase its levels at the distal end of cilia and at the base of OS-related structures formed in response to the presence of the Prph2 constructs. The restoration of these membranes, which, as the authors note, has been previously reported, is overwhelmingly the biggest effect of these constructs, and it could be argued that the restored localization, rather than degradation, of CNGbeta1 is merely a downstream consequence of the formation of these structures, with perhaps, an element of stabilization of CNGbeta1 toward degradation from direct binding to Prph2, which has also been previously reported.

RESPONSE: We agree with the reviewer. Our interpretation of our data is that the presence of Prph2 (or its variants) at the distal end of the cilia localizes CNGB1, likely due to the formation of outer segment membrane structures. Previous to this work, there was a possibility that targeting information of Prph2 was required for CNGB1. That had never been explored. We definitively rule this possibility out when we express the C-terminal tail of Prph2, which is unable to rescue CNGB1 localization. Because the tetraspanin domain of Prph2 (or ROM1) can localize CNGB1, we do agree that the definition of an outer segment structure is the driving force for CNGB1 delivery – these are new findings. We’ve restructured and added additional discussion to the manuscript to clarify this point.

The next suggested conclusion is, "Therefore, in the absence of a fully elaborated outer segment, peripherin-2's ability to delineate a disc is sufficient to drive CNG channel delivery," is partly accurate and partly misleading. If the word "localization" were to replace the term, "delivery," concerning which there are no data (aside from those confirming that Prph2 and CNGbeta1 pass through distinct secretory pathways), this statement would be an accurate summary.

RESPONSE: We have updated to “localization”, but the fact that we confirm these two proteins do not traffic together through the Golgi would suggest that delivery is independent of trafficking.

The final sentence, "Together, these data suggest that the partitioning of disc membranes from the plasma membrane by tetraspanin proteins is a key step for trafficking the CNG channel and could play a role in segregating other proteins into the plasma membrane," sentence, would also be accurate if the word "localization," were to replace the term, "trafficking." The key point for these qualifications is that the experiments presented measure steady state levels of CNGbeta1 constructs at certain locations, which are determined not only by rates of trafficking, but also rates of synthesis and degradation, and the data presented confirm that total levels of CNGbeta1 are greatly diminished in the absence of functional Prph2, rendering any conclusions about the relative roles of trafficking kinetics and degradation kinetics speculative in nature.

RESPONSE: We agree and have revised.

Aside from these major conceptual issues, there is one overriding technical question: why are almost all the experiments presented carried out with a highly over-expressed engineered version of CNGb1 with a tag, which is clearly context far from the physiological one, as opposed to examining redistribution of the endogenous CNGbeta1, which is of much greater interest. In some results relegated to a Supplemental figure (Supp. Fig. 2), the authors clearly demonstrate that sufficient signal can be obtained from immunofluorescence staining the endogenous proteins for such experiments to be readily interpretable. If the concern was cross-reactivity with non-covalently attached GARP proteins, a few experiments showing that similar results are obtained for immunostaining of the endogenous protein or of the tagged construct would haver been sufficient, and the paper could have had more physiological relevance and impact.

RESPONSE: We agree that endogenous CNG staining is important and valuable, which is why we included it in our manuscript. We were able to confirm that overexpressed CNG recapitulated the endogenous staining. We proceeded with analyzing overexpressed, tagged CNG for the reasons stated by the reviewer. Yes, cross-reactivity with soluble GARP proteins was one consideration, as was the fact that the GARP antibody is a mouse monoclonal antibody. Increased IgG due to inflammation in the RDS-/- model can obscure the outer segment region in these retinas, confounding our quantification. The tagged versions of CNGB1 and corresponding quantification offered the most clarity and continuity for the reader; therefore, we relegate the endogenous staining to the supplement.

The remaining concerns are generally of less significance and mostly conceptual or quite minor technical concerns. Technically, the imaging data and their quantification are of good quality and analyzed with reasonable rigor.

RESPONSE: Thanks!

Abstract: "In this study, we investigate how peripherin-2 is engaged in CNG channel delivery to the outer segment. Might this not be more a question of how the absence of properly formed discs impacts the formation of outer segments with plasma membranes surrounding the disks? Is this really a question of "delivery" or "lack of address to make the delivery"?

RESPONSE: Our interpretation of this comment is that it boils down to semantics. Delivery is inclusive of both trafficking and localization, which we investigate in our manuscript.

Page 3, "fluorescence complementation between peripherin-2 and CNGb1 in the inner segment of transgenic Xenopus rods (23) ". The wording is unclear. It should be stated clearly that they are describing results of "bimolecular fluorescence complementation assays" of highly overexpressed recombinant proteins expressed from transgenes.

RESPONSE: We have revised.

Page 4, "...trapped in the biosynthetic pathway," It is unclear what the authors mean by this phrase. Obviously, "biosynthesis," i.e., translation is indeed complete, but biochemical pathways are not places. Is the intention to suggest that post-translational processing, such as addition and editing of carbohydrate chains or assembly with the alpha subunit has not been completed? If so, it would be better just to say so clearly. Or, is it meant to imply that it is physically "trapped" in the ER and/or Golgi apparatus? In any case the meaning should be made clear. Co-staining with ER and Golgi markers would have been very informative with respect to the compartments in which the highly overexpressed recombinant protein is trapped.

RESPONSE: We acknowledge that our phrasing here was indirect. We have revised. Co-staining with Calnexin (an ER-marker) was attempted, but proved to be uninformative.

It should also be noted that accumulation of highly overexpressed membrane proteins within internal membranes and membrane aggregates is a very commonly observed experimental phenomenon, and not restricted to the highly specialized trafficking routes in photoreceptors.

RESPONSE: We agree that exogenous expression of membrane proteins can lead to increased presence within internal membranes of the inner segment, which we routinely see in our experiments. Importantly, our analysis is restricted to the ability of these exogenously expressed proteins to reach the ciliary compartment in Rds mice. We also conduct these experiments in wild-type retinas to ensure that our constructs are expressed, and the proteins reach the ciliary outer segment under normal conditions.

Page 4, " peripherin-2 facilitates trafficking of the CNGb1 subunit to the outer segment " The data presented to this point do not demonstrate an enhancement of transport, but only of steady-state levels. There is nothing to rule out the possibility that some beta subunit is trafficked in Rds-/-, but is unstable to degradation in the region near the cilium when peripherin-2 and outer segments are not available. An increase in transport is certainly a possible explanation for the results, but should not be taken as an unambiguous conclusion.

RESPONSE: We have altered the description of these results to allow for more interpretation of our data, which show that CNGB1 delivery to the outer segment is reduced in Rds-/- mice and enhanced when peripherin-2 is re-expressed.

Page 4, " We confirmed that the fraction of peripherin-2 that traffics conventionally through the Golgi is indeed absent in Rom1-/- retinas and found that trafficking of the CNG channel via the conventional pathway is unaffected (Figure 3A) . This is one of the stronger and more interesting results in this manuscript, and tilts the argument against trafficking as being the mechanism for enhancement by overexpressed peripherin-2 of beta subunit levels in the distal region of the photoreceptor layer.

RESPONSE: We agree.

Page 5, " Our finding that secretory trafficking of peripherin-2 and CNGb1 is distinct . Clumsy syntax- needs to be rewritten for clarity.

RESPONSE: Revised

Page 5, "two previously characterized fusion proteins... have been shown to localize to the outer segment and build a rudimentary membrane structure (19) " This previous result, which is critical to interpretation of the results in this manuscript, should be introduced early, before any experimental results using related constructs are presented, in order to avoid confusion.

RESPONSE: Prior to these experiments, we used only full-length peripherin-2, rhodopsin, or CNGB1. This paragraph is the first introduction of any chimeric protein, and we explain these two constructs thoroughly. We believe this satisfies this reviewer’s request.

Page 5, " We confirmed these data by staining for endogenous CNGb1 in Rds-/- rods electroporated with each construct (Supplemental Figure 2B,C) " This is the most informative result in this manuscript with regard to the ability of these constructs to restore proper localization of CNGB1- it is not clear that the overexpression constructs for CNGB1 present any advantage beyond stronger signal and they may not be assumed, a priori, to be faithfully reporting on interactions of Prph2 with endogenous CNGB1, which is the biologically significant question. A big problem with Supp. Fig. 2 is that there is no real control, i.e., one without any Prph2 construct electroporated. Even the Rho-Prph2CT construct has some ROS-related structures and some CNGB1 localized to the one shown at higher magnification. The Prph2-RhoCT construct seems to lead to a substantial increase in endogenous CNGB1 in inner segment membranes. This looks like a phenomenon that is potentially very interesting, although it doesn't fit with any of the models put forth in the manuscript.

RESPONSE: We agree that endogenous staining (shown in Supplemental Figure 3 of our revised manuscript) is informative, but it was technically challenging. Once we verified that our overexpression system recapitulated results for endogenous CNGB1, we went forward with the epitope-tagged CNGB1, which was clearer when quantifying CNGB1 localization to rudimentary outer segments.

Our electroporation method provides an excellent internal control, as all of the non-electroporated cells show no endogenous CNGB1 localization without peripherin expression (Sup Fig 3A).

Page 5, " cytosolic N- and C-termini of peripherin-2 are dispensable for CNGb1 outer segment localization " No- if you could simply remove them and get proper localization, that would show they are "dispensable." In these experiments they are always replaced with the corresponding region of some other protein that is localized to OS, or in one case, with 3 copies of the FLAG tag at the N-terminus. There are also clear differences in the efficacy of the different "successful" constructs, but these results and their implications are not really discussed.

RESPONSE: We make this statement in the context of these termini being dispensable to CNGB1 localization, not to peripherin-2’s stability, function, or localization. A complete truncation of either domain results in a non-functioning protein. Our supplemental data shows reduced expression with a truncated N-terminus, preventing analysis (Sup Fig 5C). The 3X-FLAG has no known function in the cell, and we believe it serves as a proxy for removing the N-terminus altogether. Removing the C-terminus would prevent proper outer segment targeting, which is key to determining how peripherin-2 impacts CNGB1 ciliary delivery. Replacing this C-terminus with an outer segment targeting domain from another protein is an established method of investigation.

Page 6, " We then wanted to determine whether the ROM1 tetraspanin region was sufficient to facilitate CNGb1 delivery by further replacing ROM1's cytoplasmic N-terminus with that of peripherin-2 (Prph2NT/CT-ROM1) . " This experiment obviously does NOT test "sufficiency" of the TM segments, as the construct has the termini replaced with the corresponding regions of Prph2, which might functionally substitute for the missing ROM1 regions.

RESPONSE: Our previous results had already ruled out a role for these termini in CNGB1 localization.

Page 6, " We show a dramatic increase in GARP staining in the aged Rds-/- retinal sections " The age dependence of this phenomenon is quite interesting and puzzling. Any thoughts on the mechanism?

RESPONSE: We agree that this natural process is very interesting. We have restructured the order of our figures and provided additional controls to support this finding. We have added this to the discussion and hope that by restructuring our manuscript, we clearly outline that we do think that membrane retention at the tip of the cilia is driving CNG channel localization and that molecularly the tetraspanin proteins play a role in organizing these membranes.

Page 6, " Although CNGα1, known to form homotetramers, can localize to the extracellular vesicles released into the outer segment area. " Not a sentence.

RESPONSE: Revised

Page 6, " Our data now shows that the population of peripherin-2 in complex with ROM1 that travels through the conventional trafficking pathway does not play a role in CNGb1 localization to the outer segment. " This is an oddly accurate, albeit somewhat contradictory sentence. Yes, you have failed to answer the question you claim this work was designed to address. Apart from this negative result, nothing is learned about trafficking, per se, from the experiments in this manuscript.

RESPONSE: Please see our response to the reviewer’s comment above that clarifies our thinking regarding our results on trafficking.

Page 7, " anticipated " Hopefully, the authors mean to say, "hypothesized," here.

RESPONSE: Revised

**Referee cross-commenting**

My impression from reading the reviewers' comments is that there is general agreement on both the strengths and the limitations of this work. In my opinion, the issues raised by the reviewers could be addressed by editing the manuscript to be more circumspect in drawing definite conclusions from data that are not fully conclusive, without necessarily adding new experiments.

Reviewer #3 (Significance (Required)):

This study addresses a problem of great interest in the photoreceptor field and in cell biology more generally of trafficking and localization of specialized membrane proteins to specialized ciliary membranes. The strengths are technical quality of data with good controls, in most cases. The limitations are largely conceptual in nature and derive from the rather simplistic approach to the experimental design, as described above. The rather dated, "mix and match" approach based on chimeric construct with pieces of sequences removed and replaced at will does not properly account for the conclusion reached many times from many experiments, including some this manuscript, that the "roles" of stretches of amino acid sequence depend exquisitely on the multidimensional context in which they are tested, not simply on their position in the linear sequence. The paper presents interesting and convincing results with respect to functional requirements for formation disc-like membranes, but very little with respect to 'trafficking."

This work has been peer reviewed in GigaScience (see https://doi.org/10.1093/gigascience/giag031), which carries out open, named peer-review. These reviews are published under a CC-BY 4.0 license and were as follows:

Reviewer 1:

The authors assembled the genomes of three Cobitis species native to Eurasia in an attempt to investigate the effects of structural variants on hybrid meiotic failure. This is certainly an interesting topic given the advances in our abilities to study hybridization that have been enabled by modern genomic sequencing methods, and the evolutionary consequences of asexually-reproducing species that result from rare instances of these hybrid events.

Major comments: The introduction of the manuscript is well-written and focused on the topic at hand. Language was mostly clear throughout the manuscript. However, the paper overall is very lengthy and would benefit from extensive revision. Personally, I think the assembly and annotation of the three genomes is worthy of being a paper (genome report) on its own. Extraction of this material into a separate manuscript would allow the authors to hone the remainder of the paper into a much more concise and focused manuscript. Some aspects of the methods section related to genome assembly and annotation could be clarified and/or bolstered. Presentation of methods is mostly clear, but the description of genome annotation methods is a bit tough to follow. This procedure included many complicated steps and may benefit from a flow chart, even if included only as a supplemental figure.

Several important quality control steps pertaining to genome assembly and DNA/RNA sequence processing were not mentioned. Authors do not report methods used for quality filtering or trimming. They do not report any process for removal of sequencing adapters. Additionally, they do not report screening of the genome assemblies for contamination from other species. These are critical steps in producing high-quality genome assemblies that need to be addressed.

Presentation of statistics describing genome assembly quality, contiguity, and completeness could be improved. Authors might want to take some inspiration from statistics required for reporting in genome reports published by other journals, such as G3 or Genome Biology and Evolution. Sequencing depth is not reported in any context for the initial assemblies. Only log-transformed values are available in a single figure. Throughout the manuscript, authors conflate sequencing coverage (the proportion of a genome or genomic region that has been sequenced) with sequencing depth (the number of times a base or genomic region has been sequenced).

For the sex-linked primers designed by the authors - I would recommend development of an internal positive control that would be expected to amplify in both sexes and be easily distinguishable from the sex-linked locus by size or fluorescent label. This allows the users to distinguish between failed PCRs and identification of the homogametic sex. This is especially important because the fish selected for marker development were collected from a relatively small portion of the species' distributions (Figure 1) so there could be population-specific differences that affect reliability of these markers for identifying sex. This is a problem I regularly encounter in my own work for wide-ranging species.

I was also surprised that the authors did not conduct a GWAS analysis. That seems to be a fairly typical analysis included in studies of this type to elucidate sex-linked SNPs. It would add to an already extensive manuscript; however, this could add an additional argument for splitting this manuscript in two. It would provide more space to include it in a more focused manuscript.

The results section contains many statements that would be more appropriate in the Methods section, or could be deleted entirely because they are redundant with statements already present in the Methods section. Additionally, there are some sentences that are more appropriate for inclusion in the Discussion section because they are interpretive. I have included examples under the 'Minor comments' section of this review. Some of the material presented as results in the Supplementary tables is presented in a confusing manner, and appears to contain errors (see examples in 'Minor comments' section below).

The first several paragraphs of the Discussion section either repeat material already covered in the Results section, or go on tangents that are not directly related to the main purpose of the paper. However, some of it could be more appropriate to include in a genome report if the authors split the manuscript in two.

Given the above issues, I find that the paper needs extensive editing and possibly more analytical work (if some of the methodological deficiencies were overlooked in the analysis phase as well as the writing phase of this project). It is unlikely this work could be accomplished in the normal window for a revision. Therefore, I regrettably suggest rejection of the manuscript.

Finally, I have no meaningful experience with FISH probes or chromosomal painting so unfortunately, I can't provide much comment on those portions of the paper.

Minor comments: Line 291: please provide specific version number for Hisat2 Line 319: version numbers for D-Genies and SyRI missing Line 331: version number for NGenomeSyn missing Line 439-440: Authors provide N50 values, but the paper would benefit from providing some additional metrics, such as N90 and L90, to help readers gauge the contiguity of these genomes. Line 442 - 443: I'm having a hard time understanding how the authors are calling these 'chromosome-level' assemblies when nearly a third (>30%) of the genome of two species (C. tanaitica and C. elongatoides) could not be assembled into chromosomal scaffolds. Line 457 - 458: Either the term 'topologically associated domains' is missing, or the authors need to remove the parentheses from around TADs if it was defined earlier in the manuscript. Line 470: change 'less' to 'fewer' Line 483 - 486: The statements that observed patterns of repeat families 'suggest' something are interpretive and should be moved to the discussion. Line 499 - 500: This sentence repeats content of the methods section. I suggest deleting it. Line 540 - 564: If I am understanding correctly, the discussion of 'coverage' here would be more accurately described as 'depth' since the authors seem to be talking about average sequencing depth in different areas of the genome. Furthermore, authors never provide untransformed measures of sequencing depth in any context (the initial genome assemblies, pool-seq data, re-sequenced individuals, etc.). Therefore, it is difficult to determine if the differences being discussed here are derived from data with enough statistical power to measure differences in sequencing depth between male and female fish. Lines 614 - 619: This could be explored with GWAS Lines 635 - 641: Much of this paragraph is a description of methods and belongs in the Methods section. Lines 664 - 667: Much of this is interpretive - more appropriate for the discussion. Lines 700 - 711: This paragraph has little or no relevance to the main topic of this paper (hybrid meiotic failure). Line 745: remove "loci's" Line 813 - 815: PMER was already defined earlier in the paper. Line 854: I suggest removal of "the first of their kind in an asexually reproducing vertebrate," because such statements rarely age well, and the concept behind the paper is interesting enough to stand on its own without pointing out the novelty of it being the 'first' time it was detected. References section: Capitalization of article titles varies from one reference to the next. Scientific names are sometimes italicized; other times they are not. Table 2: 'L50' and 'Number of Chromosomes' are always going to be integers. Why are there two significant digits to the right of the decimal point? Supplementary Figure S2: 'Cobitis' should be italicized. Supplementary Table S7: This table presents pre- and post-HiC values in a confusing manner that is nonsensical and probably erroneous. For example, the N50 values seem problematic. How do you have a 154 Kbp pre-HiC N50 contig value for C. elongatoides, but a 154 Mbp post-HiC N50 contig value for the same species? This is longer than the longest reported chromosome for any species (C. taenia) in Supplementary Table S8 (99 Mbp). Supplementary Table S10: I don't know what the percentages in line 33 refer to?

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

In this paper, Stanojcic and colleagues attempt to map sites of DNA replication initiation in the genome of the African trypanosome, Trypanosoma brucei. Their approach to this mapping is to isolate 'short-nascent strands' (SNSs), a strategy adopted previously in other eukaryotes (including in the related parasite Leishmania major), which involves isolation of DNA molecules whose termini contain replication-priming RNA. By mapping the isolated and sequenced SNSs to the genome (SNS-seq), the authors suggest that they have identified origins, which they localise to intergenic (strictly, inter-CDS) regions within polycistronic transcription units and suggest display very extensive overlap with previously mapped R-loops in the same loci. Finally, having defined locations of SNS-seq mapping, they suggest they have identified G4 and nucleosome features of origins, again using previously generated data. Though there is merit in applying a new approach to understand DNA replication initiation in T. brucei, where previous work has used MFA-seq and ChIP of a subunit of the Origin Replication Complex (ORC), there are two significant deficiencies in the study that must be addressed to ensure rigour and accuracy.

(i) The suggestion that the SNS-seq data is mapping DNA replication origins that are present in inter-CDS regions of the polycistronic transcription units of T. brucei is novel and does not agree with existing data on the localisation of ORC1/CDC6, and it is very unclear if it agrees with previous mapping of DNA replication by MFA-seq due to the way the authors have presented this correlation. For these reasons, the findings essentially rely on a single experimental approach, which must be further tested to ensure SNS-seq is truly detecting origins. Indeed, in this regard, the very extensive overlap of SNS-seq signal with RNA-DNA hybrids should be tested further to rule out the possibility that the approach is mapping these structures and not origins.

(ii) The authors' presentation of their SNS-seq data is too limited and therefore potentially provides a misleading view of DNA replication in the genome of T. brucei. The work is presented through a narrow focus on SNS-seq signal in the inter-CDS regions within polycistronic transcription units, which constitute only part of the genome, ignoring both the transcription start and stop sites at the ends of the units and the large subtelomeres, which are mainly transcriptionally silent. The authors must present a fuller and more balanced view of SNS-seq mapping, across the whole genome, to ensure full understanding and clarity.

In the revised manuscript, the authors have improved the presentation and analysis of their data, expanding the description of SNS-seq mapping across the genome, and more clearly assessing to what extent there is correlation between SNS-seq signal and previous mapping approaches to predict origins (by MFA-seq and ChiP-chip of ORC1/CDC6). With regard the correlation between SNS-seq and ORC/1CDC6 ChIP-chip, it should be noted that two datasets were generated in distinct strains of T. brucei (Lister 427 and TREU927, respectively), and it is unclear if the latter dataset can be accurately mapped to the strain used here. Notwithstanding this concern, these improvements clarify a number of aspects of the SNS-seq mapping: (1) the signal is more prevalent in the transcribed core of the genome than in the largely transcriptionally silent subtelomeres; and (2) whereas previous work revealed strong correlation between ORC1/CDC6 localisation and MFA-seq peaks at the ends of multigene transcription units, neither of these data show significant overlap with SNS-seq signal, which is not seen at transcription start or stop sites ('SSRs'; supplementary Fig.8D) and shows marked depletion at predicted ORC1/CDC6 sites (supplementary Fig.8C). To the authors' credit, they acknowledge this lack of correlation in the discussion.

The authors have not provided any new data to substantiate their assertion that SNS-seq accurately detects origins in T. brucei, and therefore the work rests on a single experimental approach, without validation. As a result, the suggestion of abundant, previously undetected origins in the intergenic regions of multigene transcription remains a prediction. One key untested limitation of the work lies in the observation that the very large majority of SNS-seq signal overlaps with previously RNA-DNA hybrids; without an experimental test, the suggestion that the authors have 'disclosed for the first time a strong link between RNANA hybrid formation and DNA replication initiation' remains conjecture.

Reviewer #2 (Public review):

Summary:

Stanojcic et al. investigate the origins of DNA replication in the unicellular parasite Trypanosoma brucei. They perform two experiments, stranded SNS-seq and DNA molecular combing. Further, they integrate various publicly available datasets, such as G4-seq and DRIP-seq, into their extensive analysis. Using this data, they elucidate the structure of origins of replications. In particular, they find various properties located at or around origins, such as polynucleotide stretches, G-quadruplex structures, regions of low and high nucleosome occupancy, R-loops, and that origins are mostly present in intergenic regions. Combining their population-level SNS-seq and their single-molecule DNA molecular combing data, they elucidate the total number of origins as well as the number of origins active in a single cell.

Between the initial submission and this revision, the raised major concerns have not been resolved, and no additional validation has been provided.

Strengths:

(1) A very strong part of this manuscript is that the authors integrate several other datasets and investigate a large number of properties around origins of replication. Data analysis clearly shows the enrichment of various properties at the origins, and the manuscript is concluded with a very well-presented model that clearly explains the authors' understanding and interpretation of the data.

(2) The DNA combing experiment is an excellent orthogonal approach to the SNS-seq data. The authors used the different properties of the two experiments (one giving location information, one giving single-molecule information) well to extract information and contrast the experiments.

(3) The discussion is exemplary, as the authors openly discuss the strengths and weaknesses of the approaches used. Further, the discussion serves its purpose of putting the results in both an evolutionary and a trypanosome-focused context.

Weaknesses:

I have major concerns about the origin of replication sites determined from the SNS-seq data. As a caveat, I want to state that, before reading this manuscript, SNS-seq was unknown to me; hence, some of my concerns might be misplaced.

(1) There are substantial discrepancies between the origins identified here and those reported in previous studies. Given that the other studies precede this manuscript, it is the authors' duty to investigate these differences. A conclusion should be reached on why the results are different, e.g., by orthogonally validating origins absent in the previous studies.

We agree that orthogonally validation of origins detected by stranded SNS-seq is necessary and we are working on it.

(2) I am concerned that up to 96% percent of all SNS-seq peaks are filtered away. If there is so much noise in the data, how can one be sure that the peaks that remain are real? Upon request, the authors have performed a control, where randomly placed peaks were run through the same filtering process. Only approximately twice as many experimental peaks passed filtering compared to random peaks. While the authors emphasize reproducibility between replicates, technical artifacts from the protocol would also be reproducible. Moreover, in other SNS-seq studies, for example, Pratto et al. Cell 2021, Fig. 1B, + and − strand peaks always appear closely paired. This pattern contrasts strongly with Fig. 2A in this manuscript.

The size and overlap of peaks depend on the length of the SNS. In our study, the width of the peaks corresponds to the size of the short nascent strands (0.5–2.5 kb) chosen as the starting material, whereas the width of the peaks in Pratto et al., Cell, 2021 are much larger (few kb). This could be due to the longer SNS used in the Pratto et al. study. Consequently, the overlap of the longer SNS is more pronounced since the SNS fibres elongate in both directions: at the 3′ end by DNA polymerase and at the 5′ end by ligation of Okazaki fragments. Additionally, the genomic regions displayed in our Figure 2A and in Pratto et al, Figure 1B are presented at substantially different resolutions, with a roughly ten‑fold difference in scale.

Further, I have some minor concerns that do not affect the main conclusions of the manuscript:

- Fig 2C: The regions shown in the heatmap have different sizes, and I presume that the regions are ordered by size on the y-axis? If so, does the cone-shaped pattern, which is origin-less for genic regions and origin-enriched for intergenic regions, arise from the size of the regions? (I.e., for each genic region, the region itself is origin-less and the flanking intergenic regions contain origins.) If this is the case, then the peaks/valleys, centered exactly on the center of the regions on the mean frequency plots, arise from the different sizes of the analyzed regions, not from the fact that origins are mostly found at the center of intergenic regions. This data would be better presented with all regions stretched to the same size. This has not been addressed in the revision.

As the reviewer suggested, we have produced scaled plots of the stranded SNS-seq origins over genic and intergenic regions (see Figure 3, which is attached along with the Reviewer #2 (Recommendations for the authors)). However, we would prefer to keep the unscaled versions in the manuscript and add a note in the text as part of the Version of Record, explaining that the origins are evenly distributed throughout intergenic regions rather than being centred within them.

- Line 123, "and the average length of origins was found to be approximately 150 bp.": To determine origins, the authors filter away overlapping peaks and peaks that are too far from each other. Both restrict the minimal and maximal length of origins that can be observed, and this, in turn, affects the average length. This has not been addressed in the revision.

This observation is correct. By applying filtering and setting the maximum distance between the positive and negative peaks, we are most likely affecting the average length by excluding potentially wider origins.

We'll modify the text as part of the Version of Record.

Are claims well substantiated?:

The identification of origins via SNS-seq appears to be incompletely supported to me.<br /> All downstream analyses depend on the reliability of origin identification.<br /> Impact:

This study has the potential to be valuable for two fields: In research focused on T. brucei as a disease agent, where essential processes that function differently than in mammals are excellent drug targets. Further, this study would impact basic research analyzing DNA replication over the evolutionary tree, where T. brucei can be used as an early-divergent eucaryotic model organism.

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

eLife Assessment

The authors use sequencing of nascent DNA (DNA linked to an RNA primer, "SNS-Seq") to localise DNA replication origins in Trypanosoma brucei, so this work will be of interest to those studying either Kinetoplastids or DNA replication. The paper presents the SNS-seq results for only part of the genome, and there are significant discrepancies between the SNS-Seq results and those from other, previously-published results obtained using other origin mapping methods. The reasons for the differences are unknown and from the data available, it is not possible to assess which origin-mapping method is most suitable for origin mapping in T. brucei. Thus at present, the evidence that origins are distributed as the authors claim - and not where previously mapped - is inadequate.

We would like to clarify a few points regarding our study. Our primary objective was to characterise the topology and genome-wide distribution of short nascent-strand (SNS) enrichments. The stranded SNS-seq approach provides the high strand-specific resolution required to analyse origins. The observation that SNS-seq peaks (potential origins) are most frequently found in intergenic regions is not an artefact of analysing only part of the genome; rather, it is a result of analysing the entire genome.

We agree that orthogonal validation is necessary. However, neither MFA-seq nor TbORC1/CDC6 ChIP-on-chip has yet been experimentally validated as definitive markers of origin activity in T. brucei, nor do they validate each other.

Public Reviews:

Reviewer #1 (Public review):

In this paper, Stanojcic and colleagues attempt to map sites of DNA replication initiation in the genome of the African trypanosome, Trypanosoma brucei. Their approach to this mapping is to isolate 'short-nascent strands' (SNSs), a strategy adopted previously in other eukaryotes (including in the related parasite Leishmania major), which involves isolation of DNA molecules whose termini contain replication-priming RNA. By mapping the isolated and sequenced SNSs to the genome (SNS-seq), the authors suggest that they have identified origins, which they localise to intergenic (strictly, inter-CDS) regions within polycistronic transcription units and suggest display very extensive overlap with previously mapped R-loops in the same loci. Finally, having defined locations of SNS-seq mapping, they suggest they have identified G4 and nucleosome features of origins, again using previously generated data.

Though there is merit in applying a new approach to understand DNA replication initiation in T. brucei, where previous work has used MFA-seq and ChIP of a subunit of the Origin Replication Complex (ORC), there are two significant deficiencies in the study that must be addressed to ensure rigour and accuracy.

(1) The suggestion that the SNS-seq data is mapping DNA replication origins that are present in inter-CDS regions of the polycistronic transcription units of T. brucei is novel and does not agree with existing data on the localisation of ORC1/CDC6, and it is very unclear if it agrees with previous mapping of DNA replication by MFA-seq due to the way the authors have presented this correlation. For these reasons, the findings essentially rely on a single experimental approach, which must be further tested to ensure SNS-seq is truly detecting origins. Indeed, in this regard, the very extensive overlap of SNS-seq signal with RNA-DNA hybrids should be tested further to rule out the possibility that the approach is mapping these structures and not origins.

(2) The authors' presentation of their SNS-seq data is too limited and therefore potentially provides a misleading view of DNA replication in the genome of T. brucei. The work is presented through a narrow focus on SNS-seq signal in the inter-CDS regions within polycistronic transcription units, which constitute only part of the genome, ignoring both the transcription start and stop sites at the ends of the units and the large subtelomeres, which are mainly transcriptionally silent. The authors must present a fuller and more balanced view of SNS-seq mapping across the whole genome to ensure full understanding and clarity.

Regarding comparisons with previous work:

- Two other attempts to identify origins in T. brucei - ORC1/CDC6 binding sites (ChIP-on-chip, PMID: 22840408) and MFA-seq (PMID: 22840408, 27228154) - were both produced by the McCulloch group. These methods do not validate each other; in fact, MFA-seq origins overlap with only 4.4% of the 953 ORC1/CDC6 sites (PMID: 29491738). Therefore, low overlap between SNS-seq peaks and ORC1/CDC6 sites cannot disqualify our findings. Similar low overlaps are observed in other parasites (PMID: 38441981, PMID: 38038269, PMID: 36808528) and in human cells (PMID: 38567819).

- We also would like to emphasize that the ORC1/CDC6 dataset originally published (PMID: 22840408) is no longer available; only a re-analysis by TritrypDB exists, which differs significantly from the published version (personal communication from Richard McCulloch). While the McCulloch group reported a predominant localization of ORC1/CDC6 sites within SSRs at transcription start and termination regions, our re-analysis indicates that only 10.3% of TbORC1/CDC6-12Myc sites overlapped with 41.8% of SSRs.

- MFA-seq does not map individual origins, it rather detects replicated genomic regions by comparing DNA copy number between S- and G1-phases of the cell cycle (PMID: 36640769; PMID: 37469113; PMID: 36455525). The broad replicated regions (0.1–0.5 Mbp) identified by MFA-seq in T. brucei are likely to contain multiple origins, rather than just one. In that sense we disagree with the McCulloch's group who claimed that there is a single origin per broad peak. Our analysis shows that up to 50% of the origins detected by stranded SNS-seq locate within broad MFA-seq regions. The methodology used by McCulloch’s group to infer single origins from MFA-seq regions has not been published or made available, as well as the precise position of these regions, making direct comparison difficult.

Finally, the genomic features we describe—poly(dA/dT) stretches, G4 structures and nucleosome occupancy patterns—are consistent with origin topology described in other organisms.

On the concern that SNS-seq may map RNA-DNA hybrids rather than replication origins: Isolation and sequencing of short nascent strands (SNS) is a well-established and widely used technique for high-resolution origin mapping. This technique has been employed for decades in various laboratories, with numerous publications documenting its use. We followed the published protocol for SNS isolation (Cayrou et al., Methods, 2012, PMID: 22796403). RNA-DNA hybrids cannot persist through the multiple denaturation steps in our workflow, as they melt at 95°C (Roberts and Crothers, Science, 1992; PMID: 1279808). Even in the unlikely event that some hybrids remained, they would not be incorporated into libraries prepared using a single-stranded DNA protocol and therefore would not be sequenced (see Figure 1B and Methods).

Furthermore, our analysis shows that only a small proportion (1.7%) of previously reported RNA-DNA hybrids overlap with SNS-seq origins. It is important to note that RNA-primed nascent strands naturally form RNA-DNA hybrids during replication initiation, meaning the enrichment of RNA-DNA hybrids near origins is both expected and biologically relevant.

On the claim that our analysis focuses narrowly on inter-CDS regions and ignores other genomic compartments: this is incorrect. We mapped and analyzed stranded SNS-seq data across the entire genome of T. brucei 427 wild-type strain (Müller et al., Nature, 2018; PMID: 30333624), including both core and subtelomeric regions. Our findings indicate that most origins are located in intergenic regions, but all analyses were performed using the full set of detected origins, regardless of location.

We did not ignore transcription start and stop sites (TSS/TTS). The manuscript already includes origin distribution across genomic compartments as defined by TriTrypDB (Fig. 2C) and addresses overlap with TSS, TTS and HT in the section “Spatial coordination between the activity of the origin and transcription”. While this overlap is minimal, we have included metaplots in the revised manuscript for clarity.

Reviewer #2 (Public review):

Summary:

Stanojcic et al. investigate the origins of DNA replication in the unicellular parasite Trypanosoma brucei. They perform two experiments, stranded SNS-seq and DNA molecular combing. Further, they integrate various publicly available datasets, such as G4-seq and DRIP-seq, into their extensive analysis. Using this data, they elucidate the structure of the origins of replication. In particular, they find various properties located at or around origins, such as polynucleotide stretches, G-quadruplex structures, regions of low and high nucleosome occupancy, R-loops, and that origins are mostly present in intergenic regions. Combining their population-level SNS-seq and their single-molecule DNA molecular combing data, they elucidate the total number of origins as well as the number of origins active in a single cell.

Strengths:

(1) A very strong part of this manuscript is that the authors integrate several other datasets and investigate a large number of properties around origins of replication. Data analysis clearly shows the enrichment of various properties at the origins, and the manuscript concludes with a very well-presented model that clearly explains the authors' understanding and interpretation of the data.

We sincerely thank you for this positive feedback.

(2) The DNA combing experiment is an excellent orthogonal approach to the SNS-seq data. The authors used the different properties of the two experiments (one giving location information, one giving single-molecule information) well to extract information and contrast the experiments.

Thank you very much for this remark.

(3) The discussion is exemplary, as the authors openly discuss the strengths and weaknesses of the approaches used. Further, the discussion serves its purpose of putting the results in both an evolutionary and a trypanosome-focused context.

Thank you for appreciating our discussion.

Weaknesses:

I have major concerns about the origin of replication sites determined from the SNS-seq data. As a caveat, I want to state that, before reading this manuscript, SNS-seq was unknown to me; hence, some of my concerns might be misplaced.

(1) I do not understand why SNS-seq would create peaks. Replication should originate in one locus, then move outward in both directions until the replication fork moving outward from another origin is encountered. Hence, in an asynchronous population average measurement, I would expect SNS data to be broad regions of + and -, which, taken together, cover the whole genome. Why are there so many regions not covered at all by reads, and why are there such narrow peaks?

Thank you for asking these questions. As you correctly point out, replication forks progress in both directions from their origins and ultimately converge at termination sites. However, the SNS-seq method specifically isolates short nascent strands (SNSs) of 0.5–2.5 kb using a sucrose gradient. These short fragments are generated immediately after origin firing and mark the sites of replication initiation, rather than the entire replicated regions. Consequently: (i) SNS-seq does not capture long replication forks or termination regions, only the immediate vicinity of origins. (ii) The narrow peaks indicate the size of selected SNSs (0.5–2.5 kb) and the fact that many cells initiate replication at the same genomic sites, leading to localized enrichment. (iii) Regions without coverage refer to genomic areas that do not serve as efficient origins in the analyzed cell population. Thus, SNS-seq is designed to map origin positions, but not the entire replicated regions.

(2) I am concerned that up to 96% percent of all peaks are filtered away. If there is so much noise in the data, how can one be sure that the peaks that remain are real? Specifically, if the authors placed the same number of peaks as was measured randomly in intergenic regions, would 4% of these peaks pass the filtering process by chance?

Maintaining the strandness of the sequenced DNA fibres enabled us to filter the peaks, thereby increasing the probability that the filtered peak pairs corresponded to origins. Two SNS peaks must be oriented in a way that reflects the topology of the SNS strands within an active origin: the upstream peak must be on the minus strand and followed by the downstream peak on the plus strand.

As suggested by the reviewer, we tested whether randomly placed plus and minus peaks could reproduce the number of filter-passing peaks using the same bioinformatics workflow. Only 1–6% of random peaks passed the filters, compared with 4–12% in our experimental data, resulting in about 50% fewer selected regions (origins). Moreover, the “origins” from random peaks showed 0% reproducibility across replicates, whereas the experimental data showed 7–64% reproducibility. These results indicate that the retainee peaks are highly unlikely to arise by chance and support the specificity of our approach. Thank you for this suggestion.

(3) There are 3 previous studies that map origins of replication in T. brucei. Devlin et al. 2016, Tiengwe et al. 2012, and Krasiļņikova et al. 2025 (https://doi.org/10.1038/s41467-025-56087-3), all with a different technique: MFA-seq. All three previous studies mostly agree on the locations and number of origins. The authors compared their results to the first two, but not the last study; they found that their results are vastly different from the previous studies (see Supplementary Figure 8A). In their discussion, the authors defend this discrepancy mostly by stating that the discrepancy between these methods has been observed in other organisms. I believe that, given the situation that the other studies precede this manuscript, it is the authors' duty to investigate the differences more than by merely pointing to other organisms. A conclusion should be reached on why the results are different, e.g., by orthogonally validating origins absent in the previous studies.

The MFA-seq data for T. brucei were published in two studies by McCulloch’s group: Tiengwe et al. (2012) using TREU927 PCF cells, and Devlin et al. (2016) using PCF and BSF Lister427 cells. In Krasilnikova et al. (2025), previously published MFA-seq data from Devlin et al. were remapped to a new genome assembly without generating new MFA-seq data, which explains why we did not include that comparison.

Clarifying the differences between MFA-seq and our stranded SNS-seq data is essential. MFA-seq and SNS-seq interrogate different aspects of replication. SNS-seq is a widely used, high-resolution method for mapping individual replication origins, whereas MFA-seq detects replicated regions by comparing DNA copy number between S and G1 phases. MFA-seq identified broad replicated regions (0.1–0.5 Mb) that were interpreted by McCulloch’s group as containing a single origin. We disagree with this interpretation and consider that there are multiple origins in each broad peaks; theoretical considerations of replication timing indicate that far more origins are required for complete genome duplication during the short S-phase. Once this assumption is reconsidered, MFA-seq and SNS-seq results become complementary: MFA-seq identifies replicated regions, while SNS-seq pinpoints individual origins within those regions. Our analysis revealed that up to 50% of the origins detected by stranded SNS-seq were located within the broad MFA peaks. This pattern—broad MFA-seq regions containing multiple initiation sites—has also recently been found in Leishmania by McCulloch’s team using nanopore sequencing (PMID: 26481451). Nanopore sequencing showed numerous initiation sites within MFA-seq regions and additional numerous sites outside these regions in asynchronous cells, consistent with what we observed using stranded SNS-seq in T. brucei. We will expand our discussion and conclude that the discrepancy arises from methodological differences and interpretation. The two approaches provide complementary insights into replication dynamics, rather than ‘vastly different’ results.

We recognize the importance of validating our results in future using an alternative mapping method and functional assays. However, it is important to emphasize that stranded SNS-seq is an origin mapping technique with a very high level of resolution. This technique can detect regions between two divergent SNS peaks, which should represent regions of DNA replication initiation. At present, no alternative technique has been developed that can match this level of resolution.

(4) Some patterns that were identified to be associated with origins of replication, such as G-quadruplexes and nucleosomes phasing, are known to be biases of SNS-seq (see Foulk et al. Characterizing and controlling intrinsic biases of lambda exonuclease in nascent strand sequencing reveals phasing between nucleosomes and G-quadruplex motifs around a subset of human replication origins. Genome Res. 2015;25(5):725-735. doi:10.1101/gr.183848.114).

It is important to note that the conditions used in our study differ significantly from those applied in the Foulk et al. Genome Res. 2015. We used SNS isolation and enzymatic treatments as described in previous reports (Cayrou, C. et al. Genome Res, 2015 and Cayrou, C et al. Methods, 2012). Here, we enriched the SNS by size on a sucrose gradient and then treated this SNS-enriched fraction with high amounts of repeated λ-exonuclease treatments (100u for 16h at 37oC - see Methods). In contrast, Foulk et al. used sonicated total genomic DNA for origin mapping, without enrichment of SNS on a sucrose gradient as we did, and then they performed a λ-exonuclease treatment. A previous study (Cayrou, C. et al. Genome Res, 2015, Figure S2, which can be found at https://genome.cshlp.org/content/25/12/1873/suppl/DC1) has shown that complete digestion of G4-rich DNA sequences is achieved under the conditions we used.

Furthermore, the SNS depleted control (without RNA) was included in our experimental approach. This control represents all molecules that are difficult to digest with lambda exonuclease, including G4 structures. Peak calling was performed against this background control, with the aim of removing false positive peaks resulting from undigested DNA structures. We explained better this step in the revised manuscript.

The key benefit of our study is that the orientation of the enrichments (peaks) remains consistent throughout the sequencing process. We identified an enrichment of two divergent strands synthesised on complementary strands containing G4s. These two divergent strands themselves do not, however, contain G4s (see Fig. 8 for the model). Therefore, the enriched molecules detected in our study do not contain G4s. They are complementary to the strands enriched with G4s. This means that the observed enrichment of

G4s cannot be an artefact of the enzymatic treatments used in this study. We added this part in the discussion of the revised manuscript.

We also performed an additional control which is not mentioned in the manuscript. In parallel with replicating cells, we isolated the DNA from the stationary phase of growth, which primarily contains non-replicating cells. Following the three λ-exonuclease treatments, there was insufficient DNA remaining from the stationary phase cells to prepare the libraries for sequencing. This control strongly indicated that there was little to no contaminating DNA present with the SNS molecules after λ-exonuclease enrichment.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Four broad issues need to be addressed.

(1) The authors have attempted to test the overlap between ORC1/CDC6 (an ORC subunit) binding in the genome and SNS-seq. If there were an overlap, this would provide evidence that the SNS-seq signals represent origins. However, the analysis provided is inadequate: merely a statement that "we obtained an overlap of 4.2% between origins and ORC1/CDC6 binding sites within a window of {plus minus}2 kb and 6.2% in the window of {plus minus}3 kb". Nowhere are these data shown or properly discussed:

a) The authors need to provide a diagram showing where in the genome the very small amount of overlapping SNS-seq and ORC1/CDC6 binding occurs, and to clearly show and state how many of the intergenic SNS-seq peaks are sites of ORC1/CDC6 binding. In the absence of such analysis, a key question is unanswered: is there any evidence of ORC1/CDC6 (or ORC more broadly) binding at the SNS-seq signals within the polycistronic transcription units?

In the original version of the manuscript, these data were already presented as percentages in the text and as a metaplot (Supplementary Fig. 8C).

We based our analysis on the set of 350 TbORC1/CDC6 binding sites available on TriTrypDB at the time of analysis. This dataset was a filtered subset of the originally reported TbORC1/CDC6 ChIP‑on‑chip peaks (personal communication, TriTrypDB). Since then, the unfiltered dataset has been made available. We therefore re‑analyzed the overlap using this dataset, to which we applied a filtering that yielded 990 binding sites closely matching the 953 sites reported by the McCulloch group. We need to stress here that the original 953 sites reported by the McCulloch group (Tiengwe et al., 2012 PMID: 22840408), is not available anymore and that the authors:

- do not provide genomic coordinates for the 953 binding sites and

- do not release any scripts or methodology that would allow independent reproduction of the 953 sites.

A similar remark also applies to the MFA-seq data (see below).

To address the reviewer’s request, we have now:

(1) Recalculated the overlap using the updated TbORC1/CDC6 dataset (990 binding sites) from TriTrypDB.

(2) Added the absolute number of overlapping SNS‑seq origins and TbORC1/CDC6 binding sites in the Results section for clarity.

(3) Included the TbORC1/CDC6 binding sites in the chromosomal overview (newly added to Supplementary Fig. 8A), so that their genomic localization relative to SNS‑seq peaks is visually accessible.

(4) Revised the metaplots of TbORC1/CDC6 distribution around SNS‑seq origins using the updated dataset (Supplementary Fig. 8C).

With these improvements, we now find that:

- Within ±2 kb, 12.9% (253) of SNS‑seq origins overlap with 25.6% of TbORC1/CDC6 binding sites.

- Within ±3 kb, 18.8% (370) of SNS‑seq origins overlap with 37.4% of TbORC1/CDC6 binding sites.

The updated metaplot shows a clear depletion of TbORC1/CDC6 signal at the origin center, with modest enrichment ~5 kb upstream and downstream. The underlying reason for this pattern remains unknown, and we agree that additional studies will be needed to understand it.

b) Equally, the authors need to explain what they conclude from this analysis. They make a comparison with T. cruzi ORC1/CDC6 and SNS-seq overlap, which does not illuminate what the data tell us. For instance, if there is no or minimal overlap between ORC1/CDC6 binding and SNS-seq peaks within the polycistronic transcription units, do they conclude that the major SNS-seq signal they detail is evidence for ORC-independent DNA replication? If there is no overlap, what further evidence can they provide that these signals truly are origins?

First, we would like to clarify that, to date, there is no evidence supporting ORC‑independent DNA replication in T. brucei, and—importantly—no published data demonstrating that TbORC1/CDC6 is universally required for DNA replication initiation. Because of this, we consider that it would be inappropriate to conclude that regions lacking detectable TbORC1/CDC6 signal undergo ORC‑independent initiation. We would prefer not to speculate in the absence of supporting evidence and would gratefully consider any reference the reviewer wishes to provide on this subject.

Second, the low overlap between TbORC1/CDC6 binding sites and SNS‑seq origins does not, in our view, invalidate our mapping of replication initiation sites. Multiple factors contribute to this:

(1) Low overlap between ORC1/CDC6 and origin‑mapping techniques has been repeatedly reported across kinetoplastids. For instance, in T. cruzi, 88.2% of origins detected by DNAscent nanopore sequencing showed no overlap with TcORC1/CDC6–Ty1 ChIP signal within ±3 kb, and only 11.7% co‑localized. This is strikingly similar to our observations in T. brucei. Thus, our data are consistent with the broader pattern in trypanosomatids rather than an exception.

(2) The origin topology detected by stranded SNS‑seq is supported by several genomic characteristic found frequently in other eukaryotes, including:

- A highly specific and polarized poly(dA)/poly(dT) sequence environment.

- Strand‑specific G4 structures positioned around origin centers.

- A conserved nucleosome‑depleted region flanked by well‑positioned nucleosomes.

These features are absent from shuffled controls, appear at high significance, and recapitulate hallmark signatures of replication origins in other eukaryotes.

Together, these findings give us confidence that the SNS‑seq peaks represent genuine origins - despite the incomplete overlap with TbORC1/CDC6 binding.

Third, we fully agree with the reviewer that a definitive conclusion would require an additional, independent validation method.

Given the lack of complete ORC subunit datasets and the unusual biology of trypanosomatid replication complexes, we believe that the cautious interpretation above is the most appropriate.

c) The authors state (Discussion): "Validation of origins is generally a difficult task, particularly in trypanosomatids, where proteins involved in the initiation of DNA replication are difficult to determine. Few proteins have been described as potential ORC subunits (reviewed in 61), and none of them have been shown to be a specific marker that indicates the origins." There are two problems with the statement. First, most of the subunits of ORC have now been described in T. brucei; the authors should make this clear. Second, mapping of ORC1/CDC6 localisation, contrary to what the authors state here, shows precise correlation with the peaks of every MFA-seq signal described (see Tiengwe et al, Cell Reports, 2012); thus, ORC1/CDC6 binding provides evidence that MFA-seq is detecting origins, something that cannot be said for SNS-seq. The authors need to correct this misleading paragraph.

As suggested, we have removed the paragraph from the Discussion to avoid confusion. However, we disagree with the reviewer's assessment and clarify below our position regarding the issues raised.

First, we agree that five candidate ORC subunits have now been identified in T. brucei. Our intention was not to suggest the contrary, but rather to emphasize that, although candidate ORC components have been described, direct functional evidence for their roles in replication initiation is still limited. For this reason, we were cautious in referring to any ORC component as a definitive marker of replication origins.

Second, regarding the reviewer’s statement that TbORC1/CDC6 binding “shows precise correlation with the peaks of every MFA‑seq signal”, we respectfully disagree based on several observations:

(1) MFA‑seq does not identify individual origin centers, but rather broad replicated regions that often span hundreds of kilobases. By design, this method cannot define the number or position of discrete origins within each peak. For that reason, MFA-seq regions do not have the resolution required to validate TbORC1/CDC6 binding sites as individual origins.

(2) In the published datasets (Tiengwe et al., Devlin et al.), no metaplots or locus‑wide quantification of the overlap between MFA‑seq peaks and TbORC1/CDC6 binding were provided. The coordinates or the approach used to define the discrete regions that they define as the originsin the MFA‑seq broad peaks have never been described or made available, making it difficult to evaluate the claimed correspondence.

(3) Notably, McCulloch’s group later reported that only 4.4% of the 953 TbORC1/CDC6 sites overlapped with their 42 MFA‑seq “origins”, underscoring that the degree of correspondence is in fact limited (PMID: 29491738).

(4) Finally, as noted in our response to point (1b), low overlap between ORC1/CDC6 binding sites and origin‑mapping techniques is a consistent observation across kinetoplastids, including T. cruzi, where DNAscent‑mapped origins show only ~12% overlap with TcORC1/CDC6 ChIP signals. This suggests that the limited overlap we observe is not unique to our dataset.

For these reasons, we are not convinced that the TbORC1/CDC6 binding sites have been shown to align precisely with MFA seq peaks, nor that these datasets definitively validate origin mapping in T. brucei. Nevertheless, to avoid over‑interpretation and potential confusion, we have removed the paragraph from the Discussion as requested. We hope this clarifies our position and improves the accuracy and neutrality of the manuscript.

(2) Like for ORC1/CDC6 localisation, the authors' evaluation of the relationship between MFA-seq and SNS-seq mapping is inadequate, and the depth of the analysis and discussion needs to be improved:

a) The authors state: "We found 28-42% stranded SNS-seq origins overlapped with early and 43-55% overlapped with late S-phase MFA-seq replicated regions (Supplementary Figure 8B)." This seems important and provides (limited) validation of both datasets, but cannot be discerned from the supplied figure. Please provide a metaplot of the two datasets centred on the MFA-seq loci, including the SNS-seq peak amplitude.

We would like to emphasize that MFA‑seq is not a method designed to map individual origins, and this fundamentally limits the interpretability of metaplots centered on MFA-seq regions. MFA‑seq identifies broad replication‑enriched domains, typically spanning 100–500 kb, within which multiple origins may fire asynchronously across the cell population.

This concern is reinforced by the original MFA‑seq publications (Tiengwe et al., 2012; Devlin et al., 2016), which:

- do not provide positional data for the 42-47 MFA‑inferred origins,

- do not describe the computational method used to derive individual origin coordinates from the broad peaks, and

- do not release any scripts or methodology that would allow independent reproduction of the claimed origin positions.

Because of this, it is not possible to reconstruct or validate how the 42 MFA‑seq “origin” sites were defined, nor to use those coordinates as anchors for metaplot analyses.

Most importantly, we disagree with the underlying assumption that each MFA‑seq peak corresponds to exactly one origin. This assumption runs counter to the principle of the technique, which identifies regions of higher DNA content in replicating cells than in non-replicating cells; it is also contradicted by our stranded SNS‑seq data and by DNA combing measurements:

- SNS‑seq detects multiple discrete origins within the same genomic regions that produce a single broad MFA‑seq peak.

- DNA combing reveals inter‑origin distances of ~36–422 kb (median ~150 kb) (PMID: 26976742), which is far shorter than the ~400–600 kb replication domains identified by MFA‑seq.

- Furthermore, with only 42 origins detected by MFA-seq, it is not possible to achieve complete genome replication in T. brucei during S-phase. DNA combing has found that the average speed of replication forks in the procyclic forms is 1.9 Kb/min. (PMID: 26976742). Dividing the size of the Trypanosoma brucei brucei TREU927 genome (26.1 Mb) by 42 origins (PMID: 22840408) shows that 621 Kb must be replicated during the S phase. Using the calculated average replication speed of 1.9 Kb/min, we can estimate that the replication of 621 Kb would take 327 min (5.45 hours) (621 Kb/1.9 Kb/min = 327 min). However, this exceeds the estimated length of the S-phase in these parasites, which is 2.31 hours (138.6 minutes) (PMID: 32397111, 31811174, 28258618) or less, 1.36 hours (PMID: 2190996, 10574712) in Trypanosoma brucei procyclic forms. Therefore, more than 42 origins are necessary to complete replication during the short S phase.

This makes it unlikely that MFA-seq regions represent single functional origins. For these reasons, a metaplot centered on MFA‑seq “loci” may lead to misinterpretations and would not provide biologically meaningful information.

We hope that the expanded explanation clarifies our interpretation of the relationship between these two complementary, but fundamentally different, methods.

b) The authors state that "Our results showed that the origins are predominantly located in the intergenic regions within the PTUs (Figure 2C)'. This finding cannot be discerned from this figure, which does not show 'strand switch regions' (SSRs; transcription start/stop sites), where MFA-seq predicts all origins to localise. The authors need to acknowledge this difference and must show a comparison of SNS-seq data, including peak amplitude, around all SSRs (whether predicted by MFA-seq to act as origins or not, since all appear to bind ORC1/CDC6).

We have now provided the metaplots showing the overlap between stranded SNS-seq origins and SSRs (see Supplementary Figure 8D). This difference has been acknowledged and discussed in the revised manuscript.

c) Finally, the authors' interpretation that around 30-55% of SNS-seq peaks overlap with MFA-seq 'origins' is highly questionable. MFA-seq peaks are regions of increased DNA content in replicating cells relative to non-replicating cells, and so the entire region under the MFA-seq peak is not necessarily an origin, but is likely to be a more discrete locus (eg, the SSR, where ORC1/CDC6 mainly localises). They should correct the wording and discuss what significance they see in this overlap; for instance, do they think SNS-seq 'clusters' are more pronounced within the MFA-seq peaks and, if so, what might this mean, and why does it not correlate with ORC1/CDC6 localisation?

As the reviewer notes, ‘MFA‑seq peaks are regions of increased DNA content, and so the entire region under the MFA-seq peak is not necessarily an origin but is likely to be a more discrete locus’. This is exactly why MFA‑seq is inappropriate for identifying discrete/individual origins: within these replicated domains, multiple origins can fire, as revealed both by stranded SNS‑seq mapping.

Regarding the overlap between SNS‑seq origins and MFA‑seq peaks, we agree with the reviewer that this overlap should not be interpreted as validating MFA‑seq “origin positions.” Instead, we now describe it more accurately as the proportion of discrete SNS‑seq origins that fall within broader MFA‑seq replication domains. This is expected, because SNS‑seq identifies individual initiation events, whereas MFA‑seq identifies S‑phase replication domains averaged across a population. Our stranded SNS‑seq data do not show enhanced origin accumulation within MFA-seq regions, and we find no correlation with TbORC1/CDC6 positions. This is now discussed.

Regarding SSRs, we do not share the view that they should be considered privileged initiation sites. After remapping the TbORC1/CDC6 ChIP‑on‑chip dataset (see above) to the T. brucei Lister 427–2018 genome (Supplementary Fig. 8A), we observed that TbORC1/CDC6 binding is distributed throughout the chromosomes, not restricted to SSRs. To quantify this, we analyzed the overlap between TbORC1/CDC6 sites and all annotated SSR classes (dSSRs, cSSRs, and head‑to‑tail regions, as defined in Kim et al. 2009). The results show that:

Only 10% of TbORC1/CDC6 binding sites fall within 40% of all SSRs.

At the level of individual SSR types:

- TTS: 3.3% of TTS overlap with 0.3% of TbORC1/CDC6 sites.

- TSS: 67% of TSS overlap with 6.1% of TbORC1/CDC6 sites.

- Head‑to‑tail regions: 54.2% overlap with 3.6% of TbORC1/CDC6 sites.

These analyses demonstrate that most TbORC1/CDC6 sites are not located at SSRs, contradicting the idea that SSRs represent primary or exclusive origin sites.

Author response image 1.

Overlap between TbORC1/CDC6-12Myc binding sites (Tiengwe 2012, Cell Reports) and strand‑switch regions (SSRs). Venn diagram showing the overlap of 990TbORC1/CDC6-12Mycbinding sites (Retrieved from TritrypDB filtered at score 22 to achieve a number of binding sites similar to the one (953 binding sites) published in Tiengwe 2012, Cell Reports) and SSR sites in the genome (Kim 2018, NAR). The intersection shows that 10.3% of Orc1/CDC6 binding sites overlap with 41.8% SSRs. The intersection is subdivided into TSS (orange), TTS in (blue) and HT in (green).

(3) A key objection to the data presentation is the decision to limit SNS-seq mapping to the intergenic regions. In addition to overlooking the SSRs (see above, 2), so-called subtelomeres, which account for nearly 50% of the T. brucei genome and are largely untranscribed, are not shown or discussed at all. Providing this data will improve clarity and also provide a key test of one of the predictions that the authors make: "most origins are localized in actively transcribed regions, which could lead to collisions between DNA replication and the transcription machinery. This spatial coincidence implies that transcription and replication must occur in a highly ordered and cooperative manner in T. brucei."

We do not understand why this reviewer concluded that we took 'the decision to limit the mapping of SNS-seq to intergenic regions'. This is a factual error.

To be clearer,

(2) We now explicitly present the distribution of SNS‑seq origins across core and subtelomeric regions in the revised Figure 2D, making clear that origin mapping was performed genome‑wide.

(2) And that SNS‑seq origins are also present in subtelomeric regions. We have revised the manuscript to avoid any implication that origin firing is restricted only to actively transcribed regions. Our data show that most SNS‑seq origins lie within intergenic regions of PTUs, but a minority are found outside these regions—including subtelomeres and SSRs. The revised text reflects this nuance and highlights that the spatial relationship between transcription and replication is strong but not exclusive.

These additions undoubtedly ensure that the genomic-wide nature of SNS-seq analysis is transparent to the reader and should therefore remove this reviewer's “key objection”.

a) The authors must show SNS-seq mapping to the subtelomeres (in addition to around the SSRs; see comment (2). If no SNS-seq peaks are detected in the subtelomeres, what do the authors conclude about how the genome is duplicated? If SNS-seq peaks are detected in the subtelomeres, do they correspond with the ordered nucleosomes in this part of the genome described by Maree et al (PMID: 28344657); if so, might SNS-seq signal localisation not be directed by transcription but chromatin?

We have now presented the proportion of origins in subtelomeric regions (see Figure 2B).

As illustrated in the metaplots in Author response image 2, the distribution of nucleosomes around the subtelomeric origins is similar to the distribution shown for all origins in the manuscript. We do not see the pattern of nucleosomes as described by Maree et al (PMID: 28344657) over ORC1/CDC6 binding sites in this part of the genome.

Author response image 2.

Metaplots showing the mean nuclesome signal over centred SNS-seq origins in subtelomeric regions. Two replicates from Maree et al 2019 (PMID: 28344657).

We never claimed that transcription directs the localisation of the SNS-seq signal. We did not conduct experiments to address this issue. In contrast, we consider that the organisation of chromatin exerts a significant influence on the selection of active origins.

(4) The major conclusion of the manuscript is that the SNS-seq signal corresponds very precisely to the locations of RNA-DNA hybrids (R-loops). Given all the limitations discussed above, can the authors rule out the possibility that SNS-seq is merely mapping DNA-DNA hybrids and is not, in fact, detecting origins?

a) It is legitimate to speculate about the possibility that the very extensive overlap between SNS-seq and DRIP-seq signals within polycistronic transcription units (between ORFs) might suggest that DRIP-seq data detects nascent strands at replication origins, rather than R-loops at sites of pre-mRNA processing, as previously suggested by Briggs et al (PMID: 30304482). (eg, 'we disclosed for the first time a strong link between R-loop formation and DNA replication initiation'; 'The RNA:DNA hybrids are formed at initiation sites by RNA priming of SNS and Okazaki fragments'). However, the authors should acknowledge that alternative explanations for the localisation and potential functions of inter-CDS R-loops have been suggested,

We do not find extensive overlap between stranded SNS-seq and DRIP-seq signal. We have observed only a minor proportion (1.7%) of the previously reported DRIP-seq signal to overlap with the origins detected by stranded SNS-seq. The RNA-primed SNS must form RNA:DNA hybrids during the initiation of DNA replication, and that an enrichment of these hybrids around the origins is expected. Therefore, we legitimately speculated that this minor proportion of RNA:DNA hybrids enriched around origin centres could be due to the origin activation.

We agree that some of the DRIP-seq signals detected around the origins may be sites of pre-mRNA processing, as previously suggested by Briggs et al. (PMID: 30304482). Since there is no data proving implication of pre-mRNA processing into DNA replication initiation we prefer not to speculate about it.

b) More importantly, the authors should provide experimental evidence that tests such a mechanistic prediction of R-loops and origins: for instance, have they attempted to remove R-loops, eg, by treatment with RNase H, and checked that the SNS-seq signal is unaltered? In the absence of such data, they cannot exclude the possibility that their work has revealed an overlooked problem with SNS-seq (which may not be limited to T. brucei; are matched DRIP-seq and SNS-seq datasets available to correlate these signals in a range of organisms?).

We have not attempted RNase H treatment for a fundamental methodological reason: it seems highly improbable that RNA:DNA hybrids would persist through the multiple denaturation steps inherent to the SNS‑seq enrichment protocol. Published biophysical measurements show that RNA:DNA hybrids melt at ~95 °C (Roberts & Crothers, Science, 1992; PMID: 1279808), which is the temperature repeatedly applied during SNS isolation. Under these conditions, persistent RNA:DNA hybrids cannot remain intact and therefore cannot be responsible for the SNS‑seq peaks detected.

We do not interpret our findings as revealing an “overlooked problem with SNS‑seq.” Instead, we consider that the enrichment of RNA:DNA hybrids around origins observed in DRIP‑seq is biologically meaningful and expected, given that replication initiation involves RNA‑primed nascent strands and that DRIP‑seq detects such structures.

Reviewer #2 (Recommendations for the authors):

I have some minor concerns that do not affect the main conclusions of the manuscript:

(1) Figure 2B: The regions shown in the heatmap have different sizes, and I presume that the regions are ordered by size on the y-axis? If so, does the cone-shaped pattern, which is origin-less for genic regions and origin-enriched for intergenic regions, arise from the size of the regions? (I.e., for each genic region, the region itself is origin-less and the flanking intergenic regions contain origins.) If this is the case, then the peaks/valleys, centered exactly on the center of the regions on the mean frequency plots, arise from the different sizes of the analyzed regions, not from the fact that origins are mostly found at the center of intergenic regions.

That is correct. The regions displayed in the heatmaps are genic and intergenic region sorted by size. We did not want to convey with this metaplot that the origins are accumulating at the centres of the intergenic region but mainly that genic regions are mostly devoid of origins and the intergenic regions enriched in origins.

(2) Line 123, "and the average length of origins was found to be approximately 150 bp.": To determine origins, the authors filter away overlapping peaks and peaks that are too far from each other. Both restrict the minimal and maximal length of origins that can be observed, and this, in turn, affects the average length.

This observation is correct. By applying filtering and setting the maximum distance between the positive and negative peaks, we are most likely affecting the average length by excluding origins that are potentially wider. Nevertheless, the violin plot shows that the majority of origins are shorter than 500 nt. In the end, the size of regions detected as the origin is not important. What gives the resolution of stranded-SNS-seq is the ability to identify the centre of the origin between the minus and plus peaks.

(3) Data in the manuscript were sometimes not presented in an easy-to-read manner. In some cases, this was due to benign things, such as missing labels for the mean frequency plots (e.g., Figure 2B, blue and green) or very small fonts for axes (Figure 2B). Sometimes, due to the plot types that were chosen, such as pie-charts (Figure 2C, see https://medium.com/analytics-vidhya/dont-use-pie-charts-in-data-analysis-6c005723e657), stacked bar plots (Figure 6B), or showing cumulative distributions (Figure 5C, and Figure 2D) it makes it difficult to judge the actual distribution.

Wherever possible, the size of the small fonts was increased to the maximum. Missing labels were added to the mean frequency plots. We increased the font size for the axes in the frequency plots.

However, we found cumulative distributions useful. If you have a more specific proposal for replacing cumulative distributions, we would be very grateful to hear it. We also hope that magnifying the figures in TIFF format with a higher resolution will improve visibility.

(4) Figure 2B: This data would be better presented with all regions stretched to the same size (the reason is explained in the public review).

We performed the scaled plots for the stranded SNS-seq origins over the genic and intergenic regions as the reviewer suggested (see Author response image 3), but we prefer to keep the unscaled versions in the manuscript.

Author response image 3.

Distribution of mapped origins in scaled genic and intergenic regions. Scaled heatmaps present the distribution of the mapped origins and shuffled controls within scaled genic and intergenic regions (± 2 kb).

(5) Line 149: "The number of origins in both cells was 148 compared using normalised mapped reads": Supplementary Figure 2D mentions that conditions were subsampled to the same amount. I would mention that explicitly in the main text ("compared using normalized, subsampled mapped reads"), as 'normalizing' would not include 'subsampling' for me. Also, I could not find the methods section that the authors refer to here.

Thanks for the suggestion. We changed the text to make this point clearer. In the methods section, the subsampling process was referred to as 'PCF down-sampling', but we changed now the name to 'Read sub-sampling' to be more consistent in the edited version of the manuscript.

(6) Figure 2C: I struggled to understand what gDNA stands for. Maybe it could be replaced with something like distribution in genome?

Thanks for this suggestion. It is changed to ‘distribution in genomic sequence’.

(7) Figure 5C: I cannot see how a G4 30 kb from an origin could be relevant. This also does not fit the scale of the author's own model at all (Figure 8).

The main goal of Figure 5C was to demonstrate the differences between origins and the nearest G4s compared to the shuffled controls. The graph shows that 50% of the origins have a G4 within 2010 bp, whereas the median for the shuffled control is 4154 bp in the case of non-stabilised G4s. Our model is based on Figure 5D, which illustrates the enrichment of G4s and poly(dA) around the centre of origins.

(8) Figure 6B: could be made supplementary in my opinion. All relevant data is repeated in panel D.

It is true that Figures 6B and 6C contain some repetition. However, we would prefer to keep Figure 6B because it provides a quantification of the six indicated categories, along with the statistical tests. Figure 6B only presents the three categories that changed significantly. Figure 6D shows distribution but does not contain quantified data.

(9) Figure 6D: This plot is repeating a lot, within single figures (Figure 6A, top) but also between figures (e.g., Figure 5D, Figure 4B). I'd prefer it if the initial plots of each figure were expanded a bit (here Figure 6A, top) to include some information from the previous figures. Then all these summary plots could be combined into a single figure at the very end (maybe still as different panels to reduce the number of lines in a single plot). Otherwise, each summary plot repeats the tracks of the previous, which becomes very repetitive.

Our model is based on these summary plots, and we calculated the relative distances between the different elements using them. Two elements were repeated in each plot: the positions of poly(dA) and G4s. These two elements served as reference points to determine the relative positions of the other elements. Following your suggestion would result again in repetitive summary plots at the end, as one combined summary plot would be overloaded with lines and difficult to understand.

(10) Figure 6D & Figure 7C: Both show predicted G4s; however, on the plus strand, one prediction has a two-peaked shape, the other only a single peak. Is this a mistake?

The graphs for the predicted G4s do not have the same shape in the two plots as they were performed in different reference genomes for T. brucei. Figure 6C is in the 427-reference genome as the MNase-seq data set was analysed in this reference genome and we re-did the SNS-seq analysis and the G4 prediction in this reference genome to be able to compare them directly. In Figure 7C we are comparing origins DRIP-seq and predicted G4s, in this case all datasets could be compared in the 427-2018 reference genome.

Author Response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The study investigates the role of vascular mural cells, specifically pericytes and vascular smooth muscle cells (vSMCs), in maintaining blood-brain barrier (BBB) integrity and regulating vascular patterning. Analyzing zebrafish pdgfrb mutants that lack brain pericytes and vSMCs, they show that mural cell deficiency does not impair BBB establishment or maintenance during larval and early juvenile stages. However, mural cells seem to be crucial for preventing vascular aneurysms and hemorrhage in adulthood as focal leakage, basement membrane disruption, and increased caveolae formation are observed in adult zebrafish at aneurysm hotspots. The authors challenge the paradigm that mural cells are essential for BBB regulation in early development while highlighting their importance for long-term vascular stability.

Strengths:

Previous studies have established that the zebrafish BBB shares molecular and morphological homology with e.g. the mammalian BBB and therefore represents a suitable model. By examining mural cell roles across different life stages - from larval to adult zebrafish - the study provides an unprecedented comprehensive developmental analysis of brain vascular development and of how mural cells influence BBB integrity and vascular stability over time. The use of live imaging, whole-brain clearing, and electron microscopy offers high-resolution insights into cerebrovascular patterning, aneurysm development, and structural changes in endothelial cells and basement membranes. By analyzing "leakage hotspots" and their association with structural endothelial defects in adults the presented findings add novel insights into how mural cell loss may lead to vascular instability.

Weaknesses:

The study uses quantitative tracer assays with multiple molecular weight dyes to evaluate blood-brain barrier (BBB) permeability. The study normalizes the intensity of tracer signals (e.g., 10 kDa, 70 kDa dextrans) in the brain parenchyma to the vascular signal of a 2000 kDa dextran tracer (assumed to remain within vessels). Intensity normalization is used to control for variations in tracer injection efficiency or vascular density. This method doesn't directly assess the absolute amount of tracer present in the parenchyma, potentially underestimating leakage severity. As the lack of BBB impairment is a "negative" finding, more rigorous controls or other methods might be needed to corroborate it.

In response to these and comments from other reviewers, we have now performed further carefully controlled analysis to test leakage of tracers using molecular weights ranging from 1 to 2000 kDa. We have performed additional normalisation approaches (new data in Fig. 2a–d) imaging tracer extravasation together with vascular reporters (Tg(kdrl:EGFP)^s843 or Tg(kdrl:Hsa.HRAS-mCherry)^s916) and used this transgenic reporter for normalisation (as suggested by Reviewer #2). The results of these experiments all supported our initial conclusions (revised Extended Data Fig. 3a–d) further validating the reliability of our method. Furthermore, as suggested by the reviewer analysis of the raw tracer intensity amounts in the parenchyma were also performed with no normalization at all (see Author response image 1). This also supports our conclusion that the BBB is intact in young animals. Finally, we now use our methods to demonstrate that we can detect an immature leaky BBB at 3 dpf and a mature functional BBB at 7 dpf (Fig. 2e-f), a suitable positive control to show that our methods and analyses are reliable.

Author response image 1.

Raw intensity values from the parenchyma confirm findings in Figure 2 and Extended Data Figure 3.a–d, Raw mean fluorescence intensity values of extravasated tracers in the midbrain.(a–b) show unnormalized values corresponding to Extended Data Fig. 3a–d, and (c–d) show unnormalized values corresponding to Fig. 1a–d. Unpaired t-tests for 70 and 10 kDa at 14 dpf in (a–b), for 10 kD at 7 dpf, and for 70 kDa at 14 dpf in (c–d). Mann-Whitney tests for 70 and 10 kDa at 7 dpf in (a–b), for 70 kDa at 7 dpf, and for 10 kDa at 14 dpf (c–d), due to non-normal distribution. These data were all generated in genotype blind assays, display variance in signal that is generated between embryos due to injection differences and show no difference between the genotypes analysed in BBB integrity. Comparison of this to normalised data using 2000 kDa tracer or kdrl expression in endothelial cells (Fig. 2 and Extended Data Fig. 3) confirms that normalisation improves the analysis, effectively controlling for embryo-to-embryo differences in delivery of tracer and imaging.

Reviewer #2 (Public review):

Summary:

The authors generated a zebrafish mutant of the pdgfrb gene. The presented analyses and data confirm previous studies demonstrating that Pdgfrb signaling is necessary for mural cell development in zebrafish. In addition, the data support previously published studies in zebrafish showing that mural cell deficiency leads to hemorrhages later in life. The authors presented quantified data on vessel density and branching, assessed tracer extravasation, and investigated the vasculature of adult mice using electron microscopy.

Strengths:

The strength of this article is that it provides independent confirmation of the important role of Pdgfrb signaling for the development of mural cells in the zebrafish brain. In addition, it confirms previous literature on zebrafish that provides evidence that, in the absence of pericytes/VSMC, hemorrhages appear (Wang et al, 2014, PMID: 24306108 and Ando et al 2021, PMID: 3431092). The study by Ando et al, 2021 did not report experiments assessing BBB leakage in pdgfrb mutants but in the review article by Ando et al (PMID: 34685412) it is stated that "indicating that endothelial cells can produce basic barrier integrity without pericytes in zebrafish."

We thank the reviewer for their comments and pointing out literature that we had not cited (this has been corrected in our revised manuscript).

As noted by other reviewers, our study goes beyond simply confirming previous literature. The quoted section by the reviewer from Ando et al 2021 regarding intact barrier integrity in pdgfrb mutants is a conclusion based on apparent lack of haemorrhages in pdgfrb mutants[1]. Our work shows haemorrhages in older animals and as such is in line with these previously published results, but it also extends previous work, for the first time reporting detailed functional analysis to assess BBB integrity. Our study uses definitive tracer assays (now including extensive revisions) to identify intact the BBB in pdgfrb mutants in live animals. This has not been previously described and is important because it offers a new perspective on the evolutionary conservation (or otherwise) of pericyte control of BBB function. Furthermore, our study investigates the nature of hotspot leakage and haemorrhages in more detail than in previous work.

Weaknesses:

(1) The authors should avoid using violin plots, which show distribution. Instead, they should replace all violin plots in the figures with graphs showing individual data points and standard deviation. For Figure 2f specifically, the standard deviation in the analyzed cohort should be shown.

This is a good point and we have replaced the violin plots with individual data points and shown all data as mean±SEM.

(2) The authors have not shown the reduced PDGFRB protein or the effect of mutation on mRNA level in their zebrafish mutant.

Our pdgfrb^uq30bh mutant allele introduces a mutation predicted to generate a truncated protein very similar to previously validated alleles (see detail in revised Extended Data Fig. 1a and methods). Our pdgfrb^uq30bh mutant also phenocopies previous pdgfrb mutants (sa16389 and um148 alleles)[2,3], displaying mural cell loss with multiple markers (Fig. 1a, new data in Extended Data Fig. 1b–c, Fig. 3b–c; Extended Data Fig. 4c–d) and the same typical morphological defects and survival rates (new data in Extended Data Fig. 1d–f). Thus our mutant phenocopy gives confidence it is most likely a null allele, in line with previous papers studying presumed null alleles[1].

We believe this provides sufficient confidence in this allele of pdgfrb. Moreover, considering that our manuscript focusses on loss of mural cells and we show definitively that this mutant has robust loss of mural cells in the brain, our mutant is suitable for this study.

(3) Statistical data analysis: Did the authors perform analyses to investigate whether the data has a normal distribution (e.g., Figures 1d, e)?

We thank the reviewer for raising this and apologise for this oversight. All data have now been assessed for normality using Shapiro-Wilk test and further statistical analyses have been performed accordingly. The specific quantifications referred to by the reviewer in Extended Data Fig. 3a–d (previously Fig. 1d-e), have normal distribution except for quantification measuring 70 kDa extravasation at 7 dpf, therefore Mann-Whitney test has been used for this comparison. Further information can be found in figure legends and methods.

(4) Analysis of tracer extravasation. The use of 2000 kDa dextran intensity as an internal reference is problematic because the authors have not provided data demonstrating that the 2000 kDa dextran signal remains consistent across the entire vasculature. The authors have not provided data demonstrating that the 2000 kDa dextran signal in vessels exhibits acceptable variance across the vasculature to serve as a reliable internal reference. The variability of this signal within a single animal remains unknown. The presented data do not address this aspect.

We thank the reviewer for their comment and agree that analysis was needed for showing 2000 kDa dextran as a reliable normalization signal.

We now show the data in the following Figures that demonstrate the consistency of signal throughout the vasculature using this 2000-kDa tracer: Extended Data Fig. 2b, Extended Data Fig. 3a and c, Extended Data Fig. 5a, Extended Data Fig. 6. In fact, we observe that this 2000 kDa tracer provides a very reliable marker of large and small calibre vessels in larval, juvenile and adult animals, even in fixed and cleared whole tissues and animals (e.g. Extended Data Fig. 2d-e, Extended Data Fig. 5 and 6).

Our further experiments and analysis support the use of this tracer as an ideal way to normalise for variation between animals and coupled with improved masking of vessels using transgenic labels (e.g. Extended Data Fig. 2b) we can quantify across whole vascular networks to reduce the concern about variation within individual animals. We also find 2000 kDa shows negligible leakage through the brain vessels Extended Data Fig. 2b–c (new data) at 2 hours post-injection (hpi) and provided images in Extended Data Fig. 6b–b′′ showing detectable signals even at 6 hpi. Finally, results generated with this approach, normalisation to transgenic markers or even raw parenchymal values of tracer intensity, generate the same conclusions. In addition, we point the reviewer to a recent pre-print that further validates this method from our team[4].

Overall, we find the use of this tracer an ideal way to normalise for differences in injection volumes between animals and we recommend the use of this method to other groups assessing BBB leakage in zebrafish.

Additionally, it's intriguing that the signal intensity in the parenchyma of the tested tracers presents a substantial range, varying by 20-30% in the analysed cohort (Figure 1g, Extended Figure 1e). Such large variability raises the question of its origin. Could it be a consequence of the normalization to 2000 kDa dextran intensity which differs between different fish? Or is it due to the differences in the parenchymal signal intensity while the baseline 2000 kDa intensity is stable? Or is the situation mixed?

This is a good point raised by the reviewer.

To address this, we have used the following approaches:

(1) We provide additional experiments and normalisation methods that support the utility of our tracer studies (new data in Fig 2a–f and Extended Data Fig. 2b–c), discussed in detail below.

(2) We provide graphs of the raw parenchymal distribution of tracer not normalised at all (also requested by reviewer 1). This is provided in Author response image 1 and further supports all our conclusions, showing that our normalisation methods generate meaningful data.

Overall, the range of parenchymal intensity that we see after tracer injection and live imaging shows variations introduced during microinjection. However, these ranges are in-line with previous publications using similar methods (see studies by O’Brown et al 2019 and 2023)[5,6], allow reliable statistical comparisons to be drawn between control and mutants and allow us to detect both immature and functional BBB states during zebrafish development (new data in Fig. 2e-f).

Of note, the variability we see is likely introduced during the injection process into tiny larval blood vessels and is the reason why we perform normalization of parenchymal tracers to a vascular dextran signal that doesn’t leak from brain vessels. In our studies, 2000-kDa dextran has been co-injected with the smaller size tracers, therefore any potential differences in injection volumes as well as imaging conditions (however consistent) should be reduced by this method.

An alternative and potentially more effective approach would be to cross the pdgfrb mutant line with a line where endothelial cells are genetically labeled to define vessels (e.g. the line kdrl used in acquiring data presented in Figure 2a). Non-injected controls could then be used as a baseline to assess tracer extravasation into the parenchyma.

We thank the reviewer for this suggestion.

In response, we have performed new tracer leakage experiments at 7 and 14 dpf in siblings and pdgfrb mutants and quantified parenchymal tracer extravasation by normalizing to vascular reporters (Tg(kdrl:EGFP)^s843 or Tg(kdrl:Hsa.HRAS-mCherry)^s916). The results were in-line with the previously presented and independent experiments and showed indistinguishable phenotypes between siblings and pdgfrb mutants (new data, Fig. 2a–d). We also used uninjected controls to assess baseline and saw consistent values approaching zero in these images and did not include this in the revised paper.

Furthermore, we have also used this approach in wild-type larvae at 3 dpf (immature BBB) and 7 dpf (functional BBB)[5]. We detected significantly higher parenchymal extravasation of 10 and 70 kDa tracers at 3 dpf compared to 7dpf, demonstrating that our method can detect leakage (new data, Fig. 2e–f).

We believe that both normalization approaches have advantages (as discussed above), therefore showing the same results with these two different approaches has further strengthened our findings.

How is the data presented in Figure 3e generated? How was the dextran intensity calculated? It looks like the authors have used the kdrl line to define vessels. Was the 2000 kDa still used as in previous figures? If not, please describe this in the Materials and Methods section.

We have moved this data to Fig. 4e (previously Fig. 3e).

Previously, we had plotted raw data due to the nature of the experiment being conducted on a vibratome sectioned tissue. The 2000 kDa tracer was not used. In response to this query and to be consistent with the new approach suggested by the reviewer, we have revised the quantification by normalizing the 10 kDa tracer extravasation to Tg(kdrl:Hsa.HRAS-mCherry)^s916) for this and the new experiments on juveniles (Fig. 5h–i). Please see the corresponding figure legends or revised methods (lines 464–472).

(5) The authors state that both controls and mutants show extravasation of 1 kDa NHS-ester into the parenchyma. However, the presented images do not illustrate this; it is not obvious from these images (Extended Data Figure 1c). Additionally, the presented quantification data (Extended Data Figure 1e) do not show that, at 7 dpf, the vasculature is permeable to this tracer. Note that the range of signal intensity of the 1 kDa NHS-ester is similar to the 70 kDa dextran (Figure 1g and Extended Figure 1e). Would one expect an increase in the ratio in case of extravasation, considering that the 2000 kDa dextran has the same intensity in all experiments? Please explain.

We thank the reviewer for raising this important point.

To clarify, we have never claimed that “2000-kDa dextran has the same intensity in all experiments”. On the contrary, vascular 2000 kDa normalization has been used to account for potential differences caused by injection, as stated in the submitted supplementary materials and now made more clear in the revision.

In response to this query, we conducted more detailed analysis on tracer extravasation patterns based on molecular weight (new data, Extended Data Fig 2b–c). This analysis showed that 1- and 10-kDa tracers have much higher extravasation rate compared to 70- and 2000-kDa tracers. Interestingly, we did not find a significant difference between 1 and 10 kDa extravasation. Therefore, in the revised manuscript we used only 10 kDa in further experiments and have removed 1 kDa from the figures.

To assess the tracers individually (new data in Extended Data Fig. 2c), parenchymal extravasation of individual tracers was normalised to their own vascular signal (eg. Mean intensity of 10 kDa in midbrain/mean intensity of 10 kDa in vasculature), to account for potential differences in injection volume. This provides a suitable method to assess leakage in wild-type animals and is now in line with how previous studies have analysed such tracer injections[5,6]. Please see revised figure legends and supplementary materials for details.

(6) The study would be strengthened by a more detailed temporal analysis of the phenotype. When do the aneurysms appear? Is there an additional loss of VSMC?

We thank the reviewer for this suggestion, and we have now performed staged imaging of the pdgfrb mutants and siblings between 7 and 21 dpf using TgBAC(acta2:EGFP)^uq17bh transgene (new data, Fig. 3b-c; Extended Data Fig. 4a–d). Consistent with previous results, acta2:EGFP-positive cells surrounding the middle mesencephalic central arteries (MMCtA) were missing in pdgfrb mutants. At 21 dpf, we have also observed a mild dilation of these vessels, likely the earliest changes to generate aneurysms (new data, Fig. 3c).

To extend the number of stages analysed in this study, we have also performed new tracer leakage experiments in juveniles (30 dpf) and found that aneurysms can be detected at this age when the 10 kDa tracer is used (new data in Fig. 5b–b′). Consistent with the adult stage phenotype, aneurysms were limited to the larger calibre vessels (arteries) in the brain. We have also observed hotspots, and upon quantification, we found fewer numbers in juveniles compared to adults, suggesting that severity of aneurysms and hotspots increase with age.

Taken together, our results show that the aneurysms in pdgfrb mutants start appearing at late larval/early juvenile stages (~21 dpf) with observable dilations. By 30 dpf, aneurysms accompanied by small numbers of hotspots are observed, which exhibits significantly increased numbers by adulthood. This also correlates with reduced development and survival rate of pdgfrb mutants after 30 dpf (new data, Extended Data Fig. 1d–e).

(7) The authors intended to analyze the BBB at later stages (line 128), but there is not a significant time difference between 2 months (Figure 2) and 3 months (Figure 3) considering that zebrafish live on average 3 years. Therefore, the selection of only two time-points, 2 and 3 months, to analyze BBB changes does not provide a comprehensive overview of temporal changes throughout the zebrafish's lifespan. How long do the pdgfb mutants live?

Respectfully, zebrafish transition from juvenile stages to adulthood between 2 and 3 months and there are many significant differences in the physiology of this organism at these two ages. At 2 months, zebrafish are still juveniles undergoing metamorphosis with rapid growth and ongoing skeletal and vascular development. By 3 months, they are sexually mature adults and have much more developed cranioskeletal and vascular systems. Having said that, we take the reviewers important point that further temporal resolution would improve the study.

We have performed new experiments in 1-month-old animals and provided comprehensive analysis of the vascular phenotypes occurring in pdgfrb mutants. These were very informative experiments analysing leakage using 10-kDa tracer injections and have significantly improved the study. We had previously provided experiments at 5-month-old adults as well (previously Fig. 4a–b and Extended Data Fig. 4a) and so now the study includes larval stages (7, 14 dpf), juveniles at 1 and 2 months and adults at 3 and 5 months. While the additional timepoints did not offer up any new conclusions, they significantly enhanced the body of work overall.

Of further note, we provided survival data up to 90 dpf where survival of the pdgfrb mutants is significantly reduced compared to siblings (Extended Data Fig. 1e). We believe this is associated with the severity of the aneurysms and haemorrhages which probably lead to lethality in these mutants.

(8) Why is there a difference in tracer permeability between 2 and 3 months (Figures 2 and 3)? Are hemorrhages not detected in 2-month-old zebrafish?

In response to this and other queries, we have added new additional experiments that provide more detailed temporal analysis on tracer accumulation (new data in Fig. 5b–c, Fig. 5f–g).

In short, we do not see obvious haemorrhages in 1- or 2-month fish at a gross level during dissections (not shown). We find that using 10-kDa tracer, we can detect small hotspots at aneurysms as early as 1 month, likely representing the earliest loss of integrity. We do not see obvious hotspots in 2-month-old animals when we use the 70-kDa tracer, this suggests to us that it is less sensitive for hotspot detection (in line with new Extended Data Fig. 2c). Finally, we find that the number of hotspots increases dramatically from Juvenile to Adult stages in our datasets, which we take as indicative of a progressive phenotype.

Overall, tracer size matters for detecting hotspots and they become more apparent in older animals - we have added a note in the main text to cover these points (lines 200–205)

(9) Figure 3: The capillary bed should be presented in magnified images as it is not clearly visible. Figure 3e shows that in the pdgfb mutant the dextran intensity is higher also in regions 6-10. How do the authors explain this?

We thank the reviewer for raising this important point.

Firstly, we now include enlarged views of the capillary beds for this experiment (Fig. 4d′) and new experiments mentioned below.

Secondly, in relation to why there is higher tracer in lateral locations and not just medial sites of haemorrhage, we believe that this is most likely due to the progressive spread of tracer from the medial hotspots. To test if this is likely, we performed additional experiments and tested tracer accumulation at 2 different timepoints in brains collected at 0.5 or 6 hpi (new data in Fig. 5f–g, Extended Data Fig. 6a–b′′). Tracer accumulation at 0.5 hpi was very minimal and was primarily limited to hotspots and nearby regions new data in (Fig. 5h), whereas a higher tracer accumulation in brains was observed across medial to lateral regions at 6 hpi (new data in Fig. 5i) in pdgfrb mutants. Comparing the data in Figure 4 (2 hpi) and new data in Figure 5i (6 hpi), the 10 kDa-tracer appears to have spread to more lateral locations given the increased time allowed post injection.

We cannot formally exclude the possibility that tracer leakage does occur slower through capillaries than at major hotspots, which might fit with the proposed model of slow leakage via increased EC transcytosis[7-9]. However, considering that we cannot detect increased tracer accumulation in pdgfrb mutants that lack aneurysms and haemorrhages at 7 and 14 dpf, such a scenario would require capillary transcytosis to be active at later juvenile and adult stages but not in larval and late larval animals. Thus, we believe the most plausible explanation is that aneurysm/haemorrhage associated leakage is the primary cause of the vascular integrity defects in zebrafish pdgfrb mutants.

We have added discussions addressing this in the revised manuscript (lines 220–230, 300–302).

(10) In general, the manuscript would benefit from a more detailed description of the performed experiments. How long did the tracer circulate in the experiments presented in Figures 2, 3, and 4?

We thank the reviewer for this suggestion and have now ensured that this is clearly described for in figure legends and methods (lines 391–395).

(11) How do the authors explain the poor signal of the 70 kDa dextran from the vasculature of 5-month-old zebrafish presented in Extended Data Figure 3?

We agree that the dextran signal was reduced compared to the other experiments in that Figure. This is likely due to sample preparation and clearing causing reduced fluorescence. Upon consideration of the presented data and the additional experiments using 10 kDa tracers providing further validations for our claims, we decided to remove this data from the paper.

(12) The study would benefit from a clear separation of the phenotypes caused by the loss of VSMC. The title eludes that also capillaries present hemorrhages which is not the case. How do vascular mural cells differ from mural cells? Are there any other mural cells?

We take the reviewers point and have now updated the title as "Mural cells protect the adult brain from haemorrhage but do not control the blood-brain barrier in developing zebrafish."

(13) I have a few comments about how the authors have interpreted the literature and why, in my opinion, they should revise their strong statements (e.g., the last sentence in the abstract).

Scientists have their own insights and interpretations of data. However, when citing published data, it should be clearly indicated whether the statement is a direct quote from the original publication or an interpretation. In the current manuscript, the authors have not correctly cited the data presented in the two published papers (references 5 and 6). These papers do not propose a model where pericytes suppress "adsorptive transcytosis" (lines 73-76). While increased transcytosis is observed in pericyte-deficient mice, the specific type of vesicular transport that is increased or induced remains unknown.

Similarly, lines 151-152 refer to references 5 and 6 and use the term "adsorptive transcytosis," but the authors of both papers did not use this term. Attributing this term to the original authors is inaccurate. Additionally, lines 152-153 do not accurately represent the findings of references 5 and 6. These papers do not state that there is an induction of "caveolae" in endothelial cells in pericyte-deficient mice. In the absence of pericytes, many vesicles can be observed in endothelial cells, but these vesicles are relatively large. It is more likely that there is some form of uncontrolled transcytosis, perhaps micropinocytosis. Please refer to the original papers accurately.

We thank the reviewer for these comments. We take the point and have rewritten the manuscript carefully to improve accuracy and avoid misrepresenting any previous claims made in specific papers.

Also, the authors have missed the fact that in mice, the extent of pericyte loss correlates with the extent of BBB leakage. To a certain extent, the remaining pericytes, can compensate for the loss by making longer processes and so ensure the full longitudinal coverage of the endothelium. This was shown in the initial work of Armulik et al (reference 5) and later in other studies.

We certainly did not miss this important point (as we are also working with these mouse models) and we now include reference to this in our expanded discussion. Of note, we do think it would be worthwhile assessing if the extent of BBB leakage and pericyte coverage also correlates with the presence of microhaemorrhages in these hypomorphic mouse models, although this is more challenging to do in mice than in zebrafish.

The bold assertion on lines 183 -187 that a lack of specific BBB phenotype in pdgfrb zebrafish mutant invalidates mouse model findings is unfounded. Despite the notion that zebrafish endothelium possesses a BBB, I present a few examples highlighting the differences in brain vascular development and why the authors' expectation of a straightforward extrapolation of mouse BBB phenotypes to zebrafish is untenable.

In mice Pdgfrb knockout is lethal, but in zebrafish, this is not the case. In marked contrast to mice, however, zebrafish pdgfrb null mutants reach adulthood despite extensive cerebral vascular anomalies and hemorrhage. Following the authors' argumentation about the unlikely divergence of zebrafish and mice evolution, does it mean that the described mouse phenotype warrants a revisit and that the Pdgfrb knockout in mice perhaps is not lethal? Another example where the role of a gene product is not one-to-one, which relates to pericyte development, is Notch3. Notch3-null mice do not show significant changes in pericyte numbers or distribution, suggesting a less prominent role in pericyte development compared to zebrafish.

Although many aspects of development are conserved between species, there are significant differences during brain vascular development between zebrafish and mice. These differences could reveal why the BBB is not impaired in zebrafish pdgfrb mutants. There is a difference in the temporal aspect when various cellular players emerge. The timing of microglia colonization in the brain differs. In mice, microglia colonization starts before the first vessel sprouts enter the brain, while in zebrafish, microglia enter after. Additionally, microglia in zebrafish and mice have a different ontogeny. In mice, astrocytes specialize postnatally and form astrocyte endfeet postnatally. In zebrafish, radial glia/astrocytes form at 48 hpf, and as early as 3 dpf, gfap+ cells have a close relationship with blood vessels. Thus, these radial glia/astrocyte-like cells could play an important role in BBB induction in zebrafish. It's worth noting that in Drosophila, the blood-brain barrier is located in glial cells. While speculative, these cells might still play a role in zebrafish, while the role of pericytes does not seem to be crucial. Pericytes enter the brain and contact with developing vasculature (endothelium) relatively late in zebrafish (60 hpf). In mice, the situation is different, as there is no such lag between endothelium and pericyte entry into the brain. I suggest that the authors approach the observed data with curiosity and ask: Why are these differences present? Are all aspects of the BBB induced by neural tissue in zebrafish? What is the contribution of microglia and astrocytes?"

Another interesting aspect to consider is the endothelial-pericyte ratio and longitudinal coverage of pericytes in the zebrafish brain, and how this relates to what is observed in mice. How similar is the zebrafish vasculature to the mouse vasculature when it comes to the average length of pericytes in the zebrafish brain? Does the longitudinal coverage of pericytes in the zebrafish brain reach nearly 100%, as it does in mice?

Based on the preceding arguments, it is recommended that the authors present a balanced discussion that provides insightful discussion and situates their work within a broader framework.

Overall, we agree with most of the points made by the reviewer above. As we have now extended the format of this paper to be a full article, we have space to provide an extended discussion and introduction. We now try to capture many of the points made by the reviewer and we think that this has significantly improved the paper. We thank the reviewer for this contribution.

We do want to point out that we did not state that our findings using zebrafish pdgfrb mutants invalidate mouse model findings. We suggest that a deeper analysis to understand the nature of the hotspots in mural cell deficient mammalian models could be very interesting in light of the zebrafish observations. We hope that the revised discussion better reflects this.

Reviewer #3 (Public review):

This manuscript examines the role of pdgfrb-positive pericytes in the establishment and maintenance of the blood-brain barrier (BBB) in the zebrafish. Previous studies in PDGFB- or PDGFRB-deficient mice have suggested that loss of pericytes results in disruption of the BBB. The authors show that zebrafish pdgfrb mutant larvae have an intact BBB and that pdgfrb mutant adult fish show large vessel defects and hemorrhage but do not exhibit substantial leakage from brain capillaries, suggesting loss of pericytes is not sufficient to "open" the BBB. The authors use beautiful and compelling images and rigorous quantification to back up most of their conclusions. The imaging of the adult brain is particularly nice. The authors rigorously document the lack of BBB leakage in pdgfrbuq30bh mutant larvae and large vessel phenotypes (eg, enlargement and rupture) in pdgfrbuq30bh mutant adults. A few points would help the authors to further strengthen their findings contradicting the current dogma from rodent models.

We appreciate the reviewer's comments on the manuscript overall and agree that addressing the raised points was needed to strengthen our findings. We have addressed the main points below and believe that this revision greatly improves this study.

Major point:

The authors document pericyte loss using a single TgBAC(pdgfrb:egfp)ncv22 transgenic line driven by the promoter of the same gene mutated in their pdgfrbuq30bh mutants. Given their findings on the consequences of pericyte loss directly contradict current dogma from rodent studies, it would be useful to further validate the absence of brain pericytes in these mutants using one of several other transgenic lines marking pericytes currently available in the zebrafish. This could be done using pdgfrb crispants, which the authors show nicely phenocopy the germline mutants, at least in larvae. This would help nail down the absence of any currently identifiable pericyte population or sub-population in the loss of pdgfrb animals and substantially strengthen the authors' conclusions.

We thank the reviewer and agree that examination of pdgfrb^uq30bh mutants using another transgenic line labelling pericytes would further validate the absence of brain pericytes. We generated a transgenic line, TgBAC(abcc9:abcc9-T2A-mCherry)^uom139, to visualise pericytes and validated the absence of brain pericytes in the pdgfrb mutants (revised Extended Data Fig. 1b). The loss of brain pericytes matched our findings using TgBAC(pdgfrb:egfp)^uq15bh line as well as previously published data by Ando et al 2016-2021, where the brain pericytes except for metencephalic artery were missing[2,3].

Other issues:

The authors should provide more information about the pdgfrbuq30bh mutant and how it was generated (including a diagram in a supplemental figure would be useful).

We thank the reviewer for this suggestion. In addition to the explanations provided in supplementary materials, we have added a schematic, provided sanger sequencing results showing the mutation as well as predicted effect of the mutation on the protein domains (Extended Data Fig. 1a).

It would be helpful to show some data on whether mutants show morphological phenotypes or developmental delay at 7 and 14 dpf, to provide some context to better assess the reduced branching and vessel length vascular phenotypes (see Figures 1c-e).

We thank the reviewer for this suggestion. We have provided further details on body length and survival of the pdgfrb mutants until 90 dpf. As reported by Ando et al 2021, we did not observe any distinguishing feature until about 30 dpf[1,3]. The adult anatomy of our mutant allele matches that of previously described null mutants and is now shown (Extended Data Fig. 1f).

If available, it would be helpful to have a positive control for the tracer leakage experiments - a genetic manipulation that does cause disruption of the BBB and leakage at 2 hours post-tracer injection (see Figures 1f and g).

We thank the reviewer for this suggestion and agree that a positive control would validate reliability of our method. We have performed new experiments at 3 dpf when BBB integrity is not yet established and at 7 dpf when BBB is functional in zebrafish[5], testing both 10 and 70 kDa tracers (new data in Fig. 2e–f). We detected significantly higher tracer accumulation at 3 dpf, showing that our methods can detect tracer leakage in the brain.

Quantification of the findings in Figure 4c, d would be useful, as would the use of germline fish for these experiments if these are now available. If this is not possible, it would be helpful to document that the crispants used in these experiments lack pdgfrb:egfp pericytes at adult stages (this is only shown for 5 dpf larvae, in Extended Data Figure 4b).

We thank the reviewer for this comment. Using TgBAC(pdgfrb:egfp)^uq15bh line, we have imaged coronal brain sections collected from 10-week old pdgfrb crispants and uninjected siblings (age-matched animals used in Fig. 5d–e, previously Fig. 4c–d). We have now included data showing that adult pdgfrb crispants lack brain mural cells, phenocopying pdgfrb^uq30bh mutants (new data, Extended Data Fig. 6f). These particular crispants are very reliable in our hands and nicely reproduce stable mutant phenotypes, giving us confidence to use the faster F0 approach in this experiment.

Adult mutants clearly show less dye leakage in the more superficial capillary regions than WT siblings, but dextran intensity is a bit higher, although this could well be diffusion from more central brain regions where overt hemorrhage is occurring. Along similar lines though, the authors' TEM data in Extended Data Figure 4d hints that there may be more caveolae in mutant brain capillaries, although the N number was lower here than for the measurements from TEM of larger central vessels (Figure 4g). It would be useful to carry out additional measurements to increase the N number in Figure 4d to see whether the difference between wild-type sibling and mutant capillary caveolae numbers remains as not significant.

We thank the reviewer for these raising important points and suggestions.

Firstly, in relation to signal in capillary regions and likely diffusion from hotspots, please see the response to reviewer 3 point 9 above.

Secondly, we have imaged and analysed more capillaries in both pdgfrb mutants and siblings (Extended Data Fig. 7a–b, previously Extended Data Fig. 4d). The results showed no significant difference between these groups, suggesting that capillary EC transcytosis is unchanged in our pdgfrb mutants.

It might be helpful to include some orienting labels and/or additional descriptions in the figure legends to help readers who are not used to looking at zebrafish brain vessels have an easier time figuring out what they are looking at and where it is in the brain.

We thank the reviewer for this suggestion and agree that adding further information in the figure legends and illustrations about orientation would make it easier for readers. In addition to the information provided in the figure legends in the submitted version, we have added an illustration, more labels on the revised figures, extended the descriptions in figure legends, main text and methods.

We have added a schematic depicting the tracer leakage assay workflow, orientation of live imaging and analysed region of interest (Extended Data Fig. 1a–b).

All figure legends have been updated with the anatomical position and microscopy view.

Additional labels on figures have been added to understand the referenced vessel names (new data in Fig. 3c and Extended Data Fig. 4a–b′).

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The study uses the intensity of tracer signals within the vessels to analyze BBB permeability, potentially underestimating leakage severity. The dye intensity is measured 2 hours after injection, however, other studies have already observed leakage after 30 Minutes, by imaging directly in the brain parenchyma. The overall intensity should also decrease through leakage from the other vessels of the body, e.g. in the trunk and tail. Probably the loss of intra-vascular dye intensity from leakage in barrier-free vessels is already so high (after 2 hours) that the smaller amount of leakage across the BBB cannot be observed.

We thank the reviewer for this comment and suggestion. We agree that small sized tracers leak from vasculature, particularly through fenestrated vessels in the trunk and tail. We have based our timing on previous studies and our own experience. In zebrafish, the study by O’Brown et al 2019 also used 2 hpi[5] for detection of leakage in mfsd2aa mutants, which also has been proposed to regulate BBB integrity by controlling EC transcytosis. Therefore, we believe that performing experiments at 2 hpi is appropriate to investigate roles of pericytes in BBB integrity. Our data would suggest that this timing works.

In response to this and other comments, we performed further experiments and analyses to test leakage of tracers testing molecular weights ranging from 1 to 2000 kDa individually. We showed that these tracers can reliably be detected in brain parenchyma and vasculature when imaged at 2 hpi. In another study, we showed that medium size tracers such as 40 kDa Dextran can be reliably detected in the vasculature in similar timepoints[10]. Considering we have performed experiments using 10 and 70 kDa tracers do detect parenchymal tracer accumulation and tracer still within the vessels, we believe this timepoint is appropriate for assessing BBB integrity in zebrafish.

In addition to these experiments, see our tracer leakage experiments in 1-month-old animals, at 0.5 and 6 hpi to test leakage pattern described above (Fig. 5 and Extended Data Fig. 6).

Therefore, the authors will need to validate their method of choice, showing an impairment of the BBB, caused by other agents (known to affect the BBB), and at 48hpf, when the BBB is not tightened yet. One example for BBB impairment can be found in O'Brown et al (2019), eLife 8e47326. doi: 10.7554/eLife.47326

We thank the reviewer for this suggestion. As shown by O’Brown et al 2019, we have performed experiments at 3 dpf when BBB integrity is not mature and at 7 dpf when BBB is functional[5], testing both 10 and 70 kDa tracers. We detected significantly higher tracer accumulation at 3 dpf, showing our new additional method (see below) can detect tracer leakage in the brain (new data in Fig. 2e–f).

Ideally, the authors would also supplement the method with additional approaches in the younger developmental stages to validate their findings.

The validation of the method and the findings is particularly important for the claims of lack of BBB impairment in the absence of mural cells, as this is a "negative" finding.

In response to this and comments from other reviewers, we performed additional tracer leakage experiments (new data in Fig. 2a–d) where we imaged 10 and 70 kDa tracers with a vascular reporter (Tg(kdrl:EGFP)^s843 or Tg(kdrl:Hsa.HRAS-mCherry)^s916) and used this reporter for normalisation. Both this approach as well as the experiments provided in the first submission (updated as Extended Data Fig. 3a–d) showed that pdgfrb mutants at 7 and 14 dpf have indistinguishable BBB integrity compared to siblings. See also Author response image 1 that further addresses this.

I also strongly suggest to rephrase and downtown the claim that vascular mural cells do not control the blood-brain barrier in developing zebrafish.

As a negative finding cannot be proven completely and lots of the previously shown effects on murine BBB impairment are rather weak (when caused by single agents such as Claudin5 deficiency or Sphingosine-phosphate receptor1 knockout), it might be important to only claim that in zebrafish no strong impairment (as observed in the mural cell-deficient mouse) could be observed. Or rephrase it to "no impairment as severe as/comparable to ... could be observed" and then provide an impairment control for the developmental stages.

We thank the reviewer for this comment and agree that negative findings are very challenging to prove. However, we find no evidence of leakage of the BBB in animals lacking mural cells at 7 and 14 dpf and believe that our data is robust on this point. As such, we believe we show that a vertebrate with a largely conserved EC BBB, can have intact barrier function in the absence of mural cells.

We have as suggested revised our claims throughout the manuscript to provide more further nuanced discussion of this, but we do not want to water down our claims too much as we believe they are important. We hope that the reviewer will appreciate our carefully worded and expanded discussion section.

Additional items of interest to the readers and therefore suggestions to improve the manuscript could be

(1) To include more molecular analysis: while the study identifies caveolae induction and basement membrane thickening as potential contributors to focal leakage, the exact molecular mechanisms linking mural cell loss to these structural changes are not deeply investigated.

(2) Also, the study primarily associates BBB disruption in the adult with aneurysms. Therefore other subtle or diffuse changes to BBB permeability that might occur even without overt vascular lesions are potentially underrepresented.

However, following up experimentally on these might exceed the scope of the manuscript.

We thank the reviewer for these suggestions and agree with both points. However, as stated by the reviewer, these experiments are beyond the scope of the manuscript and represent future directions for our lab and others.

Reviewer #2 (Recommendations for the authors):

(1) Mouse genes should be written as follows: Pdgfb, Pdgfrb and be in italics. See line line 70: it should be written "Pdgfb and Pdgfrb (italics)" and not "PdgfB and Pdgfrβ".

We have updated the text according to the reviewer’s suggestion.

(2) Please state the age of the fish analyzed in Figure 1f and 1g.

We have moved this data to Extended Fig. 3a–d (previously Fig. 1f-g) and have placed age information on the images and in the figure legends.

(3) Is the reduced vascular complexity in pdgfb mutant due to reduced angiogenesis or due to excessive pruning?

This is a good question, and we do not know at this stage. We have unpublished data that suggest pericytes secrete angiogenic growth factors, but this question warrants a thorough investigation that we believe is beyond the scope of this current study.

(4) Please check that the figure legends state the correct number of fish analysed. For example, Figure 1 d, e N=8 but there seem to be 9 data points per group - 14dpf.

We apologise for this mistake and thank the reviewer for raising this. We have updated the graphs and figure legends accordingly.

(5) Please indicate in the figures the genotypes (wt, het) of a sibling presented alongside a pdgfb mutant.

Wild-type and heterozygous mutants are commonly used together in zebrafish research as a collective control group termed siblings. Since we didn’t see any difference between wild-type and pdgfrbuq30bh/- groups in any experiments, we reported these groups together. This is now stated in the supplementary materials.

One exception to this was examination of the growth and survival rates where we show the genotypes separately (new data in Extended Data Fig. 1b-f).

(6) Please explain clearly what region is shown in Figure 2B. I do not understand the explanation "approximate location of dotted line". Is the image in the panel "a" top view of a brain?

We have moved this data to Fig. 3a′ (previously Fig. 2b) and replaced the dotted line in Figure 3a (previously Fig. 2a) with a white box indicating the location of the restricted region in the whole brain image.

We have revised the text as below:

“Subset of z-slices from the whole brain imaging in (a) and (b) (white boxes) indicating mural cell loss and abnormal capillary network patterning. 100-μm-thick maximum intensity projections (MIP) were generated using the continuation of the left middle mesencephalic central artery (MMCtA, arrow) as an anatomical landmark.”

In addition, we have updated all our figure legends clearly stating the view and anatomical position of the imaged sample.

(7) Figure 2e: Note that- the dotted areas do not correspond to the areas magnified. Please adjust.

We have moved this data to Extended Data Fig. 5a (previously Fig. 2e–e′) and updated the location of the white box in 5a shown in enlarged view in 5a′.

(8) Lines 112 and 114 - Should the indicated figure be Figure 2b-d and Figure 2c-d, respectively, and not Figure 1?

We thank the reviewer for pointing out this mistake. All the figure legends are now referred to appropriately in the revised manuscript.

(9) Data presented in Figure 2 and Figure 3 can be consolidated and presented as one Figure.

We thank the reviewer for this suggestion. After addition of new data and revising the manuscript we have decided to keep these data presented separately.

(10) Note that Figure 2a,b shows 5-month-old fish, not 2-month-old fish. Additionally, Extended Data Figure 3 shows 5-month-old fish, not 3-month-old fish.

The stages noted by the reviewer were correctly indicated.

(11) Figure 2d: Please clarify the definition of a "large vessel".

We have observed normal morphology in capillaries and noted aneurysms and hotspots in large calibre vessels such as arteries, which become more severe over time. We have revised this across the manuscript accordingly.

(12) Figure 4a, b: Please explain how the hotspots of leakage were defined based on the extravasated tracer.

Hotspots of leakage are scored when fluorescent tracer aggregates are clearly observed outside the vessels. Vessel borders were defined using the transgenic lines (Tg(kdrl:EGFP)^s843 or Tg(kdrl:Hsa.HRAS-mCherry)^s916). We have added a clear description in the methods section (lines 473–475).

Figure 4c: Why were Pdgfrb crispants used and not the mutant line?

They were used as pdgfrb crispants phenocopy the lack of brain mural cells (Extended Data Fig. 5e, previously Extended Data Fig. 4b) and mutant phenotype reliably and for practical reasons, because they allow faster experiments and reduce fish usage.

Figure 4e: The magnification of the electron microscopy images does not make it possible to clearly identify caveolae. What was the magnification of the collected images for caveolae analysis? How did the authors ensure that they quantified only caveolae and not other types of vesicles?

Respectfully, we disagree that the magnification is insufficient as our images were captured and analysed consistent with previous ultrastructural descriptions[11,12]. We based our quantification of caveolae on the size of vesicles observed and define them as circular profiles of less than 100 nm in diameter and were scored as luminal or abluminal based on proximity to each surface membrane (within 500 nm of each surface or in a thin-walled vessel the caveolae closest to each surface) (lines 398–409). Importantly, comparable analyses at similar magnifications have been independently validated in multiple caveola-deficient zebrafish genetic models[4,13]. Interestingly given the reviewers comments above, we do see increased vesicular structures that are larger than caveolae, but we only provide quantification of the caveolae here.

Reviewer #3 (Recommendations for the authors):

Congratulations to the authors on their really beautiful imaging and rigorous quantitative documentation of phenotypes - this is a really nicely done study, and could be very important to the field with just a few additional experiments to buttress the key conclusions.

We thank the reviewer for their kind comments.

In addition to the comments noted in the public review, I would only point out that there are two mislabeled call-outs in the text (Lines 112 and 114; says Figure 1, should say Figure 2).

We thank the reviewer for this point and have now revised the text accordingly.

(1) Ando, K., Ishii, T. & Fukuhara, S. Zebrafish Vascular Mural Cell Biology: Recent Advances, Development, and Functions. Life (Basel) 11 (2021). https://doi.org/10.3390/life11101041

(2) Ando, K. et al. Clarification of mural cell coverage of vascular endothelial cells by live imaging of zebrafish. Development 143, 1328-1339 (2016). https://doi.org/10.1242/dev.132654

(3) Ando, K. et al. Conserved and context-dependent roles for pdgfrb signaling during zebrafish vascular mural cell development. Dev Biol 479, 11-22 (2021). https://doi.org/10.1016/j.ydbio.2021.06.010

(4) Lim, Y. W. et al. Trans-Endothelial Trafficking in Zebrafish: Nanobio Interactions of Polyethylene Glycol-Based Nanoparticles in Live Vasculature. ACS Nano (2026). https://doi.org/10.1021/acsnano.5c21042

(5) O'Brown, N. M., Megason, S. G. & Gu, C. Suppression of transcytosis regulates zebrafish blood-brain barrier function. Elife 8 (2019). https://doi.org/10.7554/eLife.47326

(6) O'Brown, N. M. et al. The secreted neuronal signal Spock1 promotes blood-brain barrier development. Dev Cell 58, 1534-1547 e1536 (2023). https://doi.org/10.1016/j.devcel.2023.06.005

(7) Armulik, A. et al. Pericytes regulate the blood-brain barrier. Nature 468, 557-561 (2010). https://doi.org/10.1038/nature09522

(8) Daneman, R., Zhou, L., Kebede, A. A. & Barres, B. A. Pericytes are required for blood-brain barrier integrity during embryogenesis. Nature 468, 562-566 (2010). https://doi.org/10.1038/nature09513

(9) Mae, M. A. et al. Single-Cell Analysis of Blood-Brain Barrier Response to Pericyte Loss. Circ Res 128, e46-e62 (2021). https://doi.org/10.1161/CIRCRESAHA.120.317473

(10) Lim, Y.-W. et al. A Standardized Protocol to Investigate Trans- Endothelial Trafficking in Zebrafish: Nano-bio Interactions of PEG-based Nanoparticles in Live Vasculature. bioRxiv, 2025.2007.2023.666282 (2025). https://doi.org/10.1101/2025.07.23.666282

(11) Parton, R. G. & Simons, K. The multiple faces of caveolae. Nat Rev Mol Cell Biol 8, 185-194 (2007). https://doi.org/10.1038/nrm2122

(12) Parton, R. G. & del Pozo, M. A. Caveolae as plasma membrane sensors, protectors and organizers. Nat Rev Mol Cell Biol 14, 98-112 (2013). https://doi.org/10.1038/nrm3512

(13) Lim, Y. W. et al. Caveolae Protect Notochord Cells against Catastrophic Mechanical Failure during Development. Curr Biol 27, 1968-1981 e1967 (2017). https://doi.org/10.1016/j.cub.2017.05.06

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors aim to investigate the mechanisms underlying Kupffer cell death in metabolic-associated steatotic liver disease (MASLD). The authors propose that KCs undergo massive cell death in MASLD and that glycolysis drives this process. However, there appears to be a discrepancy between the reported high rates of KC death and the apparent maintenance of KC homeostasis and replacement capacity.

Strengths:

This is an in vivo study.

Weaknesses:

There are discrepancies between the authors' observations and previous reports, as well as inconsistencies among their own findings.

Before presenting the percentage of CLEC4F⁺TUNEL⁺ cells, the authors should have first shown the number of CLEC4F⁺ cells per unit area in Figure 1. At 16 weeks of age, the proportion of TUNEL⁺ KCs is extremely high (~60%), yet the flow cytometry data indicate that nearly all F4/80⁺ KCs are TIMD4⁺, suggesting an embryonic origin. If such extensive KC death occurred, the proportion of embryonically derived TIMD4⁺ KCs would be expected to decrease substantially. Surprisingly, the proportion of TIMD4⁺ KCs is comparable between chow-fed and 16-week HFHC-fed animals. Thus, the immunostaining and flow cytometry data are inconsistent, making it difficult to explain how massive KC death does not lead to their replacement by monocyte-derived cells.

We thank the reviewer for the insightful comment and the opportunity to clarify this important point. To ensure consistency between our methodologies, we replaced Clec4f staining with TIM4 staining results as requested by the reviewer. We first showed the number of TIM4⁺ cells per unit area in Figure 1B. The results showed a significant and progressive loss of TIM4⁺ cells per unit area in the liver parenchyma, decreasing from approximately 60 cells/FOV at baseline (0w) to nearly 50 at 4w and further to about 30 at 16w post-HFHC diet. This finding is fully consistent with our flow cytometry data. The percentage of the embryonically derived KC population (CD11blow F4/80hi TIM4hi) among CD45⁺ cells dropped from 30.2% (0w) to 24.3% (4w) and 17.6% (16w) (Revised Figure 1C). The absolute number per gram of liver decreased from roughly 12 x 10⁵ (1w) to 9 x 10⁵ (4w) and 5 x 10⁵ (16w) (Revised Figure 1D).

These data suggest that despite the reported high rate of cell death among CLEC4F⁺TIMD4⁺ KCs, the population appears to self-maintain, with no evidence of monocyte-derived KC generation in this model, which contradicts several recent studies in the field.

We appreciate the reviewer’s insightful comment. We agree that our data show no substantial generation of monocyte-derived Kupffer cells (MoKCs) within the 16-week HFHC model. However, we do not believe the remaining embryonic KCs(EmKCs) are maintained through self-renewal, as the proportion of Ki67⁺TIM4⁺ cells remains low at all time points (Revised Figure S2D). Instead, our observations align with a phased replacement model: recruited monocytes first differentiate into monocyte-derived macrophages (MoMFs), which we see accumulate (Revised Figure S2B, S2C), and only later adopt a KC phenotype. Consistent with this, our 16-week model shows significant EmKC loss and MoMF expansion, but not yet the emergence of TIM4-MoKCs. This timing is supported by prior studies, where TIM4-KCs were observed at 24 weeks, but not at 16 weeks, on similar diets (Ref. 1,2). Therefore, we interpret our findings as capturing an earlier phase of MASLD progression, characterized by EmKC death and MoMF accumulation, prior to their full differentiation into MoKCs.

Moreover, there is no evidence that TIM4⁺CLEC4F⁺ KCs increase their proliferation rate to compensate for such extensive cell death. If approximately 60% of KCs are dying and no monocyte-derived KCs are recruited, one would expect a much greater decrease in total KC numbers than what is reported.

Thank you for raising this point, which allows for an important clarification. The interpretation that approximately 60% of KCs are dying is correct, but this refers to the proportion of the remaining KC population at 16 weeks that is TUNEL⁺, not to 60% of the original KC pool. Since our data show that over half of the EmKCs are lost by 16 weeks (Revised Figure 1B), the 60% of dying cells at this late time point corresponds roughly to only 25-30% of the total original KC population at baseline. This distinction reconciles the high rate of apoptosis observed late in disease with the overall progressive depletion of the EmKC pool.

It is also unexpected that the maximal rate of KC death occurs at early time points (8 weeks), when the mice have not yet gained substantial weight (Figure 1B). Previous studies have shown that longer feeding periods are typically required to observe the loss of embryo-derived KCs.

We appreciate the reviewer’s insightful observation. We think KC death is a continuous event during MASLD. To induce MASH, previous studies typically assess the loss of EmKCs after longer feeding periods, which might leave us an impression that longer feeding periods are required to observe substantive loss of embryonically derived KCs. In our HFHC model, the proportion of dying KCs was already elevated by 8 weeks, and this high rate was sustained through the 16-week endpoint. In a separate MCD dietary model characterized by rapid MASLD progression, a high rate of KC death was detectable as early as 6 weeks (Revised Figure 1F). Collectively, these data suggest that the onset of significant KC death is dependent on the pace of MASLD pathogenesis, more likely an early-initiated event that is through MASLD progression.

Furthermore, it is surprising that the HFD induces as much KC death as the HFHC and MCD diets. Earlier studies suggested that HFD alone is far less effective than MASH-inducing diets at promoting the replacement of embryonic KCs by monocyte-derived macrophages.

We appreciate the reviewer’s insightful comment. In our study, we observed significant KCs death under both HFD and HFHC feeding for 20, 16 weeks, respectively. Moreover, both HFHC and HFD induced similar stages of MASLD (characterized by significant lipid accumulation without fibrosis development) by these time points (Authir response image 1). Therefore, these data support that the onset of substantial KCs death may be an early MASLD event, before the progression to MASH. Additionally, this finding aligns with existing literature showing that 16 weeks of HFD feeding alone is sufficient to cause a marked reduction in the TIM4⁺KCs population (Ref. 1).

Author response image 1.

Detection of liver fibrosis in MASLD mouse models. Male wild-type C57BL/6J mice were fed a high-fat, high-cholesterol (HFHC) diet for 16 weeks or a high-fat diet (HFD) for 20 weeks to induce MASLD. Mice fed a normal chow diet (NCD) served as controls. (A) Sirius Red staining of liver sections was performed to assess collagen deposition and fibrosis during MASLD progression. Scale bar, 20 μm. (B) Western blot analysis of liver tissue lysates showing α-smooth muscle actin (α-SMA) expression as a marker of hepatic stellate cell activation and liver fibrosis.

In Figure 2D, TIMD4 staining appears extremely faint, making the results difficult to interpret. In contrast, the TUNEL signal is strikingly intense and encompasses a large proportion of liver cells (approximately 60% of KCs, 15% of hepatocytes, 20% of hepatic stellate cells, 30% of non-KC macrophages, and a proportion of endothelial cells is also likely affected). This pattern closely resembles that typically observed in mouse models of acute liver failure. Given this apparent extent of cell death, it is unexpected that ALT and AST levels remain low in MASH mice, which is highly unusual.

Thank you for this important feedback. To address concerns about the clarity of our imaging, we have provided high-resolution split-channel raw images for Figure 2D (Revised Figure 2D), which distinctly show the localization of TIM4, TUNEL, and GS. These confirm the progressive reduction of TIM4⁺KCs and the increase in TUNEL⁺ TIM4⁺cells over time. We agree that the high proportion of TUNEL⁺cells seems at odds with the modest ALT/AST elevation. This discrepancy might be explained by the distinct nature of cell death in MASLD. Unlike the acute necrosis with membrane rupture seen in acute liver failure—which causes massive, rapid enzyme release— obesity-related liver injury is a chronic process dominated by apoptosis (Ref. 4,5). Apoptosis preserves membrane integrity until late stages (Ref. 6), with dying cells packaged into apoptotic bodies for efficient phagocytic clearance by neighboring macrophages (Ref. 7,8). This controlled disposal system minimizes the leakage of intracellular enzymes. Therefore, the coexistence of widespread apoptosis (high TUNEL signal) with limited enzyme release (low ALT/AST) is a recognized feature of chronic MASLD pathogenesis.

No statistical analysis is provided for Figure 5D, and it is unclear which metabolites show statistically significant changes in Figure 5C.

We thank the reviewer for raising this statistical problem. We have now included statistical analysis in Revised Figure 5D.

In addition, there is no evaluation of liver pathology in Clec4f-Cre × Chil1flox/flox mice. It remains possible that the observed effects on KC death result from aggravated liver injury in these animals. There is also no evidence that Chil1 deficiency affects glucose metabolism in KCs in vivo.

We thank the reviewer for these important points. We previously characterized the liver pathology of Clec4f^ΔChil1 mice in detail (preprint: eLife 2025, DOI: 10.7554/eLife.107023.1, Fig. 2). On a normal chow diet, these mice showed no differences in body weight, hepatic lipid deposition, metabolic parameters, or glucose tolerance compared to controls. However, on an HFHC diet, Clec4f^ΔChil1 mice developed significantly worse metabolic and histological phenotypes. Crucially, our in vitro data demonstrate that recombinant Chi3l1 directly reduces KC death (preprint, Fig. 6E-F), indicating that the aggravated MASLD in knockout mice is a consequence of increased KC loss, not its cause.

Regarding glucose metabolism, we have previously shown that Chi3l1 deficiency leads to increased glucose uptake by KCs in vivo using the fluorescent glucose analog 2-NBDG. This effect was reversed by supplementing knockout mice with recombinant Chi3l1 (preprint Fig. 6G-H). This provides direct evidence that Chi3l1 modulates glucose uptake in KCs in vivo.

Finally, the authors should include a more direct experimental approach to modulate glycolysis in KCs and assess its causal role in KC death in MASH.

We thank the reviewer for this constructive suggestion. To more directly evaluate the role of glycolysis in KCs death in vivo, we performed pharmacological inhibition of glycolysis using 2-deoxy-D-glucose (2-DG) in the HFHC-induced MASLD model (Revised Figure 4E–G). Wild-type mice were fed an HFHC diet for four weeks, and 2-DG (50 mg/kg) or vehicle was administered intraperitoneally every other day beginning at week 3. This short intervention period and modest dosing were chosen to limit potential systemic metabolic effects while modulating glycolytic activity during active disease development. KCs apoptosis was assessed by TIM4/TUNEL co-staining. 2-DG treatment significantly reduced the proportion of TUNEL⁺KCs compared with vehicle controls, indicating protection against KCs death. These data together with our complementary in vitro gain-of-function experiments, support a contributory role for excessive glycolytic activity in promoting KC apoptosis in MASLD. We have incorporated these findings into the revised manuscript to strengthen the causal link between glycolytic reprogramming and KCs loss in vivo (Revised manuscript, page 7, line 267-282).

Reviewer #2 (Public review):

Summary:

In this manuscript, He et al. set out to investigate the mechanisms behind Kupffer Cell death in MASLD. As has been previously shown, they demonstrate a loss of resident KCs in MASLD in different mouse models. They then go on to show that this correlates with alterations in genes/metabolites associated with glucose metabolism in KCs. To investigate the role of glucose metabolism further, they subject isolated KCs in vitro to different metabolic treatments and assess cleaved caspase 3 staining, demonstrating that KCs show increased Cl. Casp 3 staining upon stimulation of glycolysis. Finally, they use a genetic mouse model (Chil1KO) where they have previously reported that loss of this gene leads to increased glycolysis and validate this finding in BMDMs (KO). They then remove this gene specifically from KCs (Clec4fCre) and show that this leads to increased macrophage death compared with controls.

Strengths:

As we do not yet understand why KCs die in MASLD, this manuscript provides some explanation for this finding. The metabolomics is novel and provides insight into KC biology. It could also lead to further investigation; here, it will be important that the full dataset is made available.

Weaknesses:

Different diets are known to induce different amounts of KC loss, yet here, all models examined appear to result in 60% KC death. One small field of view of liver tissue is shown as representative to make these claims, but this is not sufficient, as anything can be claimed based on one field of view. Rather, a full tissue slice should be included to allow readers to really assess the level of death.

Thank you for raising this point regarding data presentation. We analyzed full tissue slices and found that including a view of the entire slice at a standard magnification makes individual KC difficult to resolve (Author response image 2). To clearly represent the extent and distribution of KCs death across the liver tissue slice, we now include lower-magnification images that provide a wider field of view, allowing readers to assess the pattern across a larger tissue area (Revised Figures 1, 2, 6F).

Author response image 2.

Assessment of KCs death on full liver tissue slice. (A) Immunofluorescence staining was performed to detect Kupffer cell (KC) death in liver sections from mice fed an MCD diet for 6 weeks. Cell death was assessed by TUNEL staining (green), and KCs were identified by TIM4 staining (red). Nuclei were counterstained with DAPI (blue). Representative whole-tissue view is shown. Scale bars, 1mm.

Additionally, there is no consistency between the markers used to define KCs and moMFs, with CLEC4F being used in microscopy, TIM4 in flow, while the authors themselves acknowledge that moKCs are CLEC4F+TIM4-. As moKCs are induced in MASLD, this limits interpretation. Additionally, Iba1 is referred to as a moMF marker but is also expressed by KCs, which again prevents an accurate interpretation of the data. Indeed, the authors show 60% of KCs are dying but only 30% of IBA1+ moMFs, as KCs are also IBA1+, this would mean that KCs die much more than moMFs, which would then limit the relevance of the BMDM studies performed if the phenotype is KC specific. Therefore, this needs to be clarified.

We thank the reviewer for the constructive comments. For consistency, we have standardized our KC marker to TIM4 for all immunostaining data, aligning it with our flow cytometry analysis (Revised Figures 1, 2D, 6F). We have also clarified that IBA1 is expressed by hepatic macrophages (both KCs and MoMFs)(Revised Figure 2C, Revised manuscript, page 5, lines 182-183). Moreover, we also included the clarification that 60% of TIM4⁺ KCs are TUNEL⁺ versus 30% of total IBA1⁺ cells further supports that KCs undergo death more readily than MoMFs (Revised manuscript, page 5, lines 186-189). We also acknowleged the limitation of BMDM studies in the Revised manuscript, page 8, line 332-340.

The claim that periportal KCs die preferentially is not supported, given that the majority of KCs are peri-portal. Rather, these results would need to be normalised to KC numbers in PP vs PC regions to make meaningful conclusions.

We thank the reviewer for this important point. We included the normalized data. At 8 weeks, the normalized death rate was significantly higher in periportal versus pericentral regions (p = 0.041), supporting increased periportal KC susceptibility during early MASLD. By 16 weeks, proportional death rates became comparable between zones (Revised Figure 2D, Revised manuscript, page 6, lines 194-201).

Additionally, KCs are known to be notoriously difficult to keep alive in vitro, and for these studies, the authors only examine cl. Casp 3 staining. To fully understand that data, a full analysis of the viability of the cells and whether they retain the KC phenotype in all conditions is required.

We appreciate the reviewer’s suggestions. To confirm the identity and health of isolated KCs in our in vitro studies, we showed that ~95% of primary isolated KCs are TIM4⁺ (Revised Figure S3A). Furthermore, Calcein-AM staining confirmed that the remaining KCs under our experimental conditions are viable and healthy (Revised Figure S4A).

Finally, in the Cre-driven KO model, there does not seem to be any death of KCs in the controls (rather numbers trend towards an increase with time on diet, Figure 6E), contrary to what had been claimed in the rest of the paper, again making it difficult to interpret the overall results.

We thank the reviewer for this comment. During our analysis, we indeed observed no reduction in KCs in the Clec4f cre control mice. This prompted us to consider that Cre insertion itself might influence KCs mainteinence. To investigate this, we performed TIM4/Ki67 co-staining, which revealed significantly higher numbers of proliferating KCs in Clec4f cre mice compared with C57BL/6J mice under NCD. Following HFHC feeding, KCs proliferation in Clec4f cre mice increased even further. These results indicate that Cre insertion enhanced KCs self-renewal in Clec4f cre mice，which contributes to maintenance of the KCs pool during MASLD (Revised Figures S8A and S8B). (Revised manuscript, page 9, line 363-370).

Additionally, there is no validation that the increased death observed in vivo in KCs is due to further promotion of glycolysis.

We thank the reviewer for this constructive suggestion. To more directly evaluate the role of glycolysis in KCs death in vivo, we performed pharmacological inhibition of glycolysis using 2-deoxy-D-glucose (2-DG) (Revised Figure 4E–G). Wild-type mice were fed an HFHC diet for five weeks, and 2-DG (50 mg/kg) or vehicle was administered intraperitoneally every other day beginning at week 3. This short intervention period and modest dosing were chosen to limit potential systemic metabolic effects while modulating glycolytic activity in KCs. KCs apoptosis was assessed by TIM4/TUNEL co-staining. 2-DG treatment significantly reduced the proportion of TUNEL⁺KCs compared with vehicle controls, indicating protection against KCs death. These data, together with our complementary in vitro gain-of-function experiments support a contributory role for excessive glycolytic activity in promoting KCs death in MASLD. We have incorporated these findings into the revised manuscript to strengthen the causal link between glycolytic reprogramming and KCs loss in vivo (Revised manuscript, page 7, line 267-282).

Reviewer #3 (Public review):

This manuscript provides novel insights into altered glucose metabolism and KC status during early MASLD. The authors propose that hyperactivated glycolysis drives a spatially patterned KC depletion that is more pronounced than the loss of hepatocytes or hepatic stellate cells. This concept significantly enhances our understanding of early MASLD progression and KC metabolic phenotype.

Through a combination of TUNEL staining and MS-based metabolomic analyses of KCs from HFHC-fed mice, the authors show increased KC apoptosis alongside dysregulation of glycolysis and the pentose phosphate pathway. Using in vitro culture systems and KC-specific ablation of Chil1, a regulator of glycolytic flux, they further show that elevated glycolysis can promote KC apoptosis.

However, it remains unclear whether the observed metabolic dysregulation directly causes KC death or whether secondary factors, such as low-grade inflammation or macrophage activation, also contribute significantly. Nonetheless, the results, particularly those derived from the Chil1-ablated model, point to a new potential target for the early prevention of KC death during MASLD progression.

The manuscript is clearly written and thoughtfully addresses key limitations in the field, especially the focus on glycolytic intermediates rather than fatty acid oxidation. The authors acknowledge the missing mechanistic link between increased glycolysis and KC death. Still, several interpretations require moderation to avoid overstatement, and certain experimental details, particularly those concerning flow cytometry and population gating, need further clarification.

Strengths:

(1) The study presents the novel observation of profound metabolic dysregulation in KCs during early MASLD and identifies these cells as undergoing apoptosis. The finding that Chil1 ablation aggravates this phenotype opens new avenues for exploring therapeutic strategies to mitigate or reverse MASLD progression.

(2) The authors provide a comprehensive metabolic profile of KCs following HFHC diet exposure, including quantification of individual metabolites. They further delineate alterations in glycolysis and the pentose phosphate pathway in Chil1-deficient cells, substantiating enhanced glycolytic flux through 13C-glucose tracing experiments.

(3) The data underscore the critical importance of maintaining balanced glucose metabolism in both in vitro and in vivo contexts to prevent KC apoptosis, emphasizing the high metabolic specialization of these cells.

(4) The observed increase in KC death in Chil1-deficient KCs demonstrates their dependence on tightly regulated glycolysis, particularly under pathological conditions such as early MASLD.

Weaknesses:

(1) The novelty is questionable. The presented work has considerable overlap with a study by the same lab, which is currently under review (citation 17), and it should be considered whether the data should not be presented in one paper.

We appreciate the reviewer for the opportunity to clarify the relationship between the two studies. In our previous work (citation 17), we focused on the transcriptional metabolic differences between Kupffer cells (KCs) and monocyte-derived macrophages (MoMFs) and identified Chi3l1 as a selective protective factor that limits glucose uptake and shields KCs from metabolic stress–induced cell death, with minimal effects on MoMFs. That study directly motivated the current work. The observation that KCs are uniquely protected from metabolic stress led us to hypothesize that excessive glycolytic activation itself may be a primary driver of KCs death, which forms the central question of the present study. Accordingly, the current manuscript shifts the focus from Chi3l1-mediated protection to the mechanistic role of hyperglycolysis in driving KCs mortality, using distinct experimental approaches and addressing a different biological question. Because the two studies address conceptually distinct aims—one defining a protective regulator of KCs survival and the other dissecting glycolysis-driven KCs death mechanisms—we believe they are best presented as separate manuscripts. Combining them into a single study would dilute the mechanistic depth and clarity of each story.

(2) The authors report that 60% of KCs are TUNEL-positive after 16 weeks of HFHC diet and confirm this by cleaved caspase-3 staining. Given that such marker positivity typically indicates imminent cell death within hours, it is unexpected that more extensive KC depletion or monocyte infiltration is not observed. Since Timd4 expression on monocyte-derived macrophages takes roughly one month to establish, the authors should consider whether these TUNEL-positive KCs persist in a pre-apoptotic state longer than anticipated. Alternatively, fate-mapping experiments could clarify the dynamics of KC death and replacement.

We thank the reviewer for this astute observation. As shown in revised Figure 2D, the proportion of TIM4⁺TUNEL⁺KCs peaks at 8 weeks after HFHC feeding and remains elevated at 16 weeks. However, examination of the corresponding single-channel TIM4 staining during this period reveals that the overall density of TIM4⁺ KCs does not undergo abrupt or synchronous depletion. This temporal dissociation between sustained TUNEL positivity and relatively gradual KCs loss suggests that TUNEL-positive KCs do not undergo immediate clearance. Based on these observations, we agree with the reviewer that a substantial fraction of TUNEL-positive KCs likely persists in a prolonged pre-apoptotic or stressed state rather than undergoing rapid cell death. This interpretation is consistent with the absence of extensive KCs depletion or compensatory monocyte infiltration at these time points. Importantly, previous studies (Ref. 1,2) indicate that KCs are eventually lost as MASLD progresses, supporting the notion that KC death is a gradual process that unfolds over an extended time frame rather than acutely.

(3) The mechanistic link between elevated glycolytic flux and KC death remains unclear.

We thank the reviewer for this constructive suggestion. To more directly evaluate the role of glycolysis in KCs death in vivo, we performed pharmacological inhibition of glycolysis using 2-deoxy-D-glucose (2-DG) (Revised Figure 4E–G). Wild-type mice were fed an HFHC diet for five weeks, and 2-DG (50 mg/kg) or vehicle was administered intraperitoneally every other day beginning at week 3. This short intervention period and modest dosing were chosen to limit potential systemic metabolic effects while modulating glycolytic activity of KCs. KCs apoptosis was assessed by TIM4/TUNEL co-staining. 2-DG treatment significantly reduced the proportion of TUNEL⁺KCs compared with vehicle controls, indicating protection against KCs death. These data, together with our complementary in vitro gain-of-function experiments, support a contributory role for excessive glycolytic activity in promoting KC apoptosis in MASLD. We have incorporated these findings into the revised manuscript to strengthen the causal link between glycolytic reprogramming and KCs loss in vivo (Revised manuscript, page 7, line 267-282).

(4) The study does not address the polarization or ontogeny of KCs during early MASLD. Given that pro-inflammatory macrophages preferentially utilize glycolysis, such data could provide valuable insight into the reason for increased KC death beyond the presented hyperreliance on glycolysis.

We thank the reviewer for this insightful comment. Regarding KCS ontogeny, flow cytometry analysis (Revised Figure 1C) shows that KCs remain uniformly TIM4^hi during early MASLD, indicating that monocyte-derived KCs (TIM4^low) have not yet emerged at these stages. To address KCs polarization, we assessed the expression of M1-type (pro-inflammatory) markers (Nos2, Cxcl9, CIITA, Cd86, Ccl3, and Ccl5) and M2-type (anti-inflammatory) markers (Chil3, Retnla, Arg1, and Mrc1) in KCs isolated from WT mice fed a HFHC diet for 0, 8, and 16 weeks. As shown in revised Figure S5A, M1 markers progressively increase over time, whereas M2 markers remain unchanged or slightly decrease. This polarization shift is consistent with the increased glycolytic activity observed in KCs during early MASLD. Together, these data indicate that embryonically derived KCs undergo a pro-inflammatory polarization accompanied by enhanced glycolytic metabolism during early MASLD, providing mechanistic context for their increased susceptibility to metabolic stress–induced cell death beyond hyperreliance on glycolysis alone (Revised manuscript, page 7-8, line 307-321).

(5) The gating strategy for monocyte-derived macrophages (moMFs) appears suboptimal and may include monocytes. A more rigorous characterization of myeloid populations by including additional markers would strengthen the study's conclusions.

We thank the reviewer for raising this important point. To improve the rigor of our analysis, we adopted gating strategies established in previous studies (PMID: 41131393; PMID: 32562600). Specifically, Kupffer cells were defined as CD45⁺CD11b⁺F4/80^hi TIM4^hi cells, while monocyte-derived macrophages (MoMFs) were defined as CD45⁺Ly6G^-CD11b⁺F4/80^low TIM4^low/− cells, thereby excluding contaminating neutrophils and minimizing inclusion of circulating monocytes. Using this refined gating strategy, we observed a progressive reduction of KCs accompanied by a corresponding increase in MoMFs in WT mice during HFHC feeding (Revised Figures 1C and S2B–C), (Revised manuscript, page 4, line 154-163).

(6) While BMDMs from Chil1 knockout mice are used to demonstrate enhanced glycolytic flux, it remains unclear whether Chil1 deficiency affects macrophage differentiation itself.

We thank the reviewer for this important question. To determine whether Chi3l1 deficiency affects macrophage differentiation, we analyzed the expression of M1-type (pro-inflammatory) markers (Nos2, Cxcl9, CIITA, Cd86, Ccl3, and Ccl5) and M2-type (anti-inflammatory) markers (Chil3, Retnla, Arg1, and Mrc1) in Kupffer cells isolated from WT and Chil1^-/- mice fed a HFHC diet for 0, 8, and 16 weeks. At baseline (0 weeks), Chi3l1 deficiency was associated with elevated expression of multiple M1 markers, whereas M2 marker expression was comparable between WT and Chil1^-/- KCs. During MASLD progression, the pro-inflammatory signature in Chil1^-/- KCs was further enhanced, while anti-inflammatory marker expression became dysregulated (revised Figure S5C). Together, these data indicate that Chi3l1 deficiency does not impair macrophage differentiation per se but biases KCs toward a partially pro-inflammatory, M1-like phenotype, providing additional context for the enhanced glycolytic flux observed in Chi3l1-deficient macrophages (Revised manuscript, page 7-8, line 307-321).

(7) The authors use the PDK activator PS48 and the ATP synthase inhibitor oligomycin to argue that increased glycolytic flux at the expense of OXPHOS promotes KC death. However, given the high energy demands of KCs and the fact that OXPHOS yields 15-16 times more ATP per glucose molecule than glycolysis, the increased apoptosis observed in Figure 4C-F could primarily reflect energy deprivation rather than a glycolysis-specific mechanism.

We thank the reviewer for highlighting this important point. We agree that KCs are highly metabolically active and that perturbations of OXPHOS can influence overall cellular energy balance. As noted in our response to comment #3, we further performed glycolysis inhibition assay by 2-DG in vivo, the protection of KCs observed following 2-DG in vivo (Revised Figure 4E-G) further provides evidence that increased glycolytic flux is not merely correlated with, but functionally contributes to KCs loss in

MASLD.

(8) In Figure 1C, KC numbers are significantly reduced after 4 and 16 weeks of HFHC diet in WT male mice, yet no comparable reduction is seen in Clec4Cre control mice, which should theoretically exhibit similar behavior under identical conditions.

We thank the reviewer for this comment. During our analysis, we indeed observed no reduction in KCs in the Clec4f cre control mice. This prompted us to consider that Cre insertion itself might influence KCs mainteinence. To investigate this, we performed TIM4/Ki67 co-staining, which revealed significantly higher numbers of proliferating KCs in Clec4f cre mice compared with C57BL/6J mice under NCD. Following HFHC feeding, KCs proliferation in Clec4f cre mice increased even further. These results indicate that Cre insertion enhanced KCs self-renewal in Clec4f cre mice，which contributes to maintenance of the KCs pool during MASLD (Revised Figures S8A and S8B). (Revised manuscript, page 9, line 363-370).

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

To address the concerns raised in the public review, the authors should:

(1) Reassess their conclusions using the same panels in flow and microscopy, e.g., the combination of CLEC4F, TIM4, and IBA1. This will allow resKCs (CLEC4F+TIM4+IBA1+), moKCs (CLEC4F+TIM4-IBA1+), and moMFs (CLEC4F-TIM4-IBA1+) to be accurately defined and hence their viability and numbers correctly assessed.

We thank the reviewer for this insightful suggestion. In our flow cytometry analysis, we did not detect a CD45⁺CD11b^lowF4/80^hiTIM4^low population, indicating that monocyte-derived KCs (moKCs) have not emerged in our model at this stage. To more accurately quantify resident KCs (resKCs) in the current study, we replaced CLEC4F with TIM4 staining and enumerated TIM4⁺as well as TIM4⁺TUNEL⁺ cells. These data were highly consistent with CLEC4F⁺TUNEL⁺cell counts, confirming that moKCs are not involved in KCs death during early MASLD (Revised Figure 1A,B,E,F).

(2) Investigate why the number of KCs in controls and MASLD are so distinct between Figures 1 and 6.

We appreciate the reviewer’s suggestions. Like we explained above, Cre insertion promotes KCs self-renewal (Revised manuscript, Figure S8). This enhanced proliferative capacity likely accounts for the relative preservation of KCs numbers in Clec4f-Cre mice during HFHC feeding, explaining the apparent discrepancy with WT mice (Revised manuscript, Figure 6D-E).

(3) Normalise the tunel+ cells based on the number of KCs in PP vs PC regions.

After normalizing KCs death to KCs numbers in periportal (PP) versus pericentral (PC) regions, we found the proportion was significantly higher in PV regions compared to CV regions at 8 weeks of HFHC feeding. We have therefore revised our texts. (Revised manuscript, page 5, lines 194-201).

(4) Demonstrate the viability of KCs in vitro across conditions.

To confirm the identity and health of isolated KCs in our in vitro studies, we show that ~95% of primary isolated KCs are TIM4⁺ (Revised Figure S3A). Furthermore, Calcein-AM staining confirmed that the remaining KCs under our experimental conditions are viable and healthy (Revised Figure S4A).

(5) Confirm previous studies demonstrating different degrees of KC loss depending on the model of MASLD.

We thank the reviewer for highlighting this point. Consistent with previous studies, KCs loss has been reported to varying degrees depending on the MASLD model used, reflecting the heterogeneity of hepatic macrophages, marker choice, mouse husbandry, and diet regimen. For example, in a 6-week MCD feeding model, ~10% of CLEC4F⁺ KCs were TUNEL⁺ (Figure 4A, Ref. 9). Another 6-week MCD study reported a drop from 66% to 26% TIM4⁺ KCs (Figure 2A, Ref. 12). In an HFD model, TIM4⁺ KCs decreased by ~20% after 16 weeks (Figure 1G, Ref. 1). In a Western diet model, TIM4⁺KCs decreased by >50% at 36 weeks (Figures 1J and 2C, Ref. 2). Together, these studies underscore the model-dependent nature of KCs loss and highlight the importance of experimental context and marker selection when assessing KCs dynamics in MASLD. We have included these studies in our discussion section (Revised manuscript, page 9-10, line 393-402)

(6) Demonstrate in vivo that loss of CHIL1 drives further glycolysis in KCs.

In Figure 6G-H of our previous study, we showed that Chi3l1 deficiency leads to more glucose uptake by KCs in vivo whereas suppelementing KO mice with recombinant Chi3l1 will significantly reduced glucose uptake by KCs through treating mice with a fluorescent glucose analog 2-NBDG. We included the related figure here as Author response image 3.

Author response image 3.

Chi3l1 limits glucose uptake by Kupffer cells in vivo. (A) Measurement of 2-NBDG (a fluorescent glucose analog) uptake by KCs in vivo. WT and Chil1^-/- mice, either untreated or supplemented with rChi3l1, were injected intraperitoneally with 12 mg/kg 2-NBDG. After 45mins, KCs were isolated and glucose uptake assessed by spectrophotometry. (B) Representative immunofluorescence images of liver sections stained for TIM4 (red) and 2-NBDG uptake (green) to visualize glucose uptake by KCs in situ. Scale bar = 10 µm (zoom). Quantification is shown as the percentage of TIM4⁺ cells that are also 2-NBDG⁺. Representative images were shown in B. One-way ANOVA was performed in A, B. P value is as indicated.

(7) There is no mention of the publication of the metabolomics dataset; this should be released with the manuscript.

We included the raw metabolomics dataset as Table S1 and S2 now.

Reviewer #3 (Recommendations for the authors):

(1) Methods: Reconsider which methods are described in the main text versus the Supplementary Information to improve readability and consistency.

Thank you for your valuable suggestion. We have reevaluated and adjusted the placement of the methods section between the main text and the supplementary materials.

(2) Line 34: Check for grammar issues.

L34 has been revised as follows : Additionally, using Chi3l1-deficient mice, we further demonstrated that increased glucose utilization accelerates KCs death in vivo.

(3) Lines 101, 110: Explicitly reference the corresponding Supplementary Methods sections.

We have included the references for these two methods sections (Revised supplementary materials and methods, Line 30, 65, respectively).

(4) Figure 2: Iba1 marks all macrophages, not only monocyte-derived macrophages; both figure and text (line 205) require correction.

We have corrected Iba1 represent hepatic macrophages including both KCs and MoMFs (Revised Figure 2C, manuscript page 5, line 182).

(5) Line 218-219: Avoid overinterpretation, as only KCs, hepatocytes, and hepatic stellate cells were assessed - not all hepatic populations.

We appreciate the reviewer’s valuable suggestion and rephrased our description accordingly (Revised manuscript, page 5, line 186-189).

(6) Line 262: Use abbreviations consistently throughout the manuscript.

We have gone through the whole manuscript and double checked the abbreviations.

(7) Line 264: Include the palmitic acid (PA) concentration used.

We included 800 µM PA in the revised manuscript (Revised manuscript, page 6, line 250).”

(8) Lines 316-317: Check for grammar errors.

Grammar errors are checked (Revised manuscript, page 8, line 340-341).

(9) Line 337-338: See comment above on gating strategy.

We updated gating strategy accordingly (Revised manuscript, page 9, line 361-362).

(10) Line 343-344: Note that Chi3l1 is not exclusively expressed by KCs.

We rephrased our words accordingly (Revised manuscript, page 9, line 374-378).

(11) Lines 355-358: The statement that "sustained glycolytic hyperactivation culminates not in sustained activation, but in apoptotic cell death" is unsupported by data or literature, as macrophage polarization was not analyzed in this study.

We removed the statement from the revised manuscript.

(12) Lines 375-379: Rephrase to clarify that while KCs are metabolically active and glucose-demanding, excessive glycolytic flux accelerates apoptosis.

We have rephrased to clarify (Revised Manuscript, page 10, lines 405-407).

(13) Lines 375-385 & 387-397: Consolidate overlapping statements for conciseness and coherence.

We have consolidate the overlapping statements (Revised manuscript, page 10, lines 405-425).

Reference

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Remmerie, A. et al. Osteopontin Expression Identifies a Subset of Recruited Macrophages Distinct from Kupffer Cells in the Fatty Liver. Immunity 53, 641-657.e614, doi:10.1016/j.immuni.2020.08.004 (2020).

Ozer, J., Ratner, M., Shaw, M., Bailey, W. & Schomaker, S. The current state of serum biomarkers of hepatotoxicity. Toxicology 245, 194-205, doi:10.1016/j.tox.2007.11.021 (2008).

Malhi, H. & Gores, G. J. Molecular mechanisms of lipotoxicity in nonalcoholic fatty liver disease. Semin Liver Dis 28, 360-369, doi:10.1055/s-0028-1091980 (2008).

Ibrahim, S. H., Hirsova, P. & Gores, G. J. Non-alcoholic steatohepatitis pathogenesis: sublethal hepatocyte injury as a driver of liver inflammation. Gut 67, 963-972, doi:10.1136/gutjnl-2017-315691 (2018).

Kerr, J. F., Wyllie, A. H. & Currie, A. R. Apoptosis: a basic biological phenomenon with wide-ranging implications in tissue kinetics. British journal of cancer 26, 239-257, doi:10.1038/bjc.1972.33 (1972).

Poon, I. K., Lucas, C. D., Rossi, A. G. & Ravichandran, K. S. Apoptotic cell clearance: basic biology and therapeutic potential. Nat Rev Immunol 14, 166-180, doi:10.1038/nri3607 (2014).

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Author response:

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

Public Reviews:

Reviewer #1 (Public review):

In this manuscript, the authors aimed to identify the molecular target and mechanism by which α-Mangostin, a xanthone from Garcinia mangostana, produces vasorelaxation that could explain the antihypertensive effects. Building on prior reports of vascular relaxation and ion channel modulation, the authors convincingly show that large-conductance potassium BK channels are the primary site of action. Using electrophysiological, pharmacological, and computational evidence, the authors achieved their aims and showed that BK channels are the critical molecular determinant of mangostin's vasodilatory effects, even though the vascular studies are quite preliminary in nature.

Strengths:

(1) The broad pharmacological profiling of mangostin across potassium channel families, revealing BK channels - and the vascular BK-alpha/beta1 complex - as the potently activated target in a concentration-dependent manner.

(2) Detailed gating analyses showing large negative shifts in voltage-dependence of activation and altered activation and deactivation kinetics.

(3) High-quality single-channel recordings for open probability and dwell times.

(4) Convincing activation in reconstituted BKα/β1-Ca_v nanodomains mimicking physiological conditions and functional proof-of-concept validation in mouse aortic rings.

We thank the reviewer for acknowledging the strength of the different aspects investigated in our study.

Weaknesses are minor:

(1) Some mutagenesis data (e.g., partial loss at L312A) could benefit from complementary structural validation.

In the attempt to improve structural insight for the presented mutagenesis data, we have used Alphafold3 (AF3; Abramson et al., 2024) to generate models of the I308A, L312M and A316P substitutions and repeated the docking for each (Fig. R1). According to these predictive models,

The I308A substitution considerably straightens the S6 helix starting at this residue. Hence, all residues are displaced relative to the WT: C_a of L312, F315, and A316 are displaced by 2.8 Å, 4.2 Å, and 4.6 Å, respectively, widening the bottom of the binding pocket. However, the prediction confidence is rated lower as in the other AF3 models for all helices (70 > plDDT > 50). In the docking, poses in the binding pocket comparable to these observed in the WT (i.e. involving I308A, L312 and A316) and with the same molecule orientation have higher binding energies (-7.13 to -6.66 kcal mol^-1). Additionally, poses without contact to I308A arise that have a more vertical position, indicating that the structural change affects the binding region.

The changes induced by L312M are localized to residues 313-323, where S6 bends towards S5. Binding energies are lower especially in the best 2 poses that are also most comparable to the WT docking (-9.88 kcal mol^-1), but clustering overall is poor and poses are more heterogeneous. Interactions with L312M are completely abolished, while interactions with I308 (in 11/20 poses), F315 (in all poses), and A316 (in 5/20 poses) persist. Because of the rather small structural alteration induced by the substitution and the variable poses one could speculate that the reduced V_½ shift is due to the observed loss in binding to L312M; however, retained interactions to the other residues would still allow α-Mangostin to activate.

A316P induces a displacement of the S6 helix compared to the WT while the other pore helices are not affected. S6 shows an enhanced outward bending around A316, which results in displacements of residues where a-Mangostin would bind, i.e., the C_a of F315 and L312M are displaced by 2.4 Å and 2.8 Å (I308 is not affected). Residues below are moved in a more rotational way, resulting in a C_a displacement of 3.1 Å for Y318 and even 5.7 Å for V319, before displacements decrease again towards the intracellular helix end. While interactions with A316P are present in 10/20 analyzed poses, the helix displacement seems to hinder I308 and L312 interactions, as the best docked a-Mangostin pose (-8.41 kcal mol^-1) is predicted to only contact F315 and Y318, and overall, any I308 or L312 contacts only occurred in 3/20 and 7/20 poses (wildtype: 17/20 and 20/20 poses). This may hint at a mechanism where A316P probably has a substantial allosteric share in reducing the V_½ shift induced by a-Mangostin and underlines the exceptional effect of this mutation (i.e., complete loss of a V_½ shift).

Author response image 1.

Alphafold3 models of BK I308A, L312M, and A316P with α-Mangostin docked to the mutant structures. The upper row shows an overview of the mutant pore helices (AF3 models) used for molecular docking. The lower row shows the binding region with the wildtype structure overlaid in gray. Only 3 helices are shown for clarity.

Although these results provide interesting tentative explanations for the effect of the mutations and conclusions from AF3 models become increasingly robust, we think that definitive statements of their mechanistic contributions would require experimental studies of mutant channels, i.e., cryo-EM or crystallography, that are beyond our means. Therefore, we have decided not to include this data in the manuscript; however, it is accessible for the interested reader within the public review. Hopefully, as cryo-EM structures have been obtained for the wildtype channel, there will be studies on mutations of this gating-relevant S6 segment in the future.

(2) While Cav-BK nanodomains were reconstituted, direct measurement of calcium signals after mangostin application onto native smooth muscle could be valuable.

We are not sure if a global elevation of cellular calcium concentration would be informative. We rather expect that the relevant local Ca²⁺ elevation would occur as sparks in the BK-Ca_v nanodomains, close to the membrane. We would anticipate a change in spark duration, as the Ca²⁺ inward current would be stopped faster by the enhanced repolarization via a-Mangostin activated BKα/β1 channels. This would require fast Ca²⁺ imaging acquisition speed to capture spark activity. We concur that this would be an informative experiment to investigate a more native situation. However, we would have to accomplish such methodologically challenging measurements in a separate project, which could fruitfully be combined with a more extensive characterization of aortic contraction as also suggested in the following remark (3).

(3) The work has an impact on ion channel physiology and pharmacology, providing a mechanistic link between a natural product and vasodilation. Datasets include electrophysiology traces, mutagenesis scans, docking analyses, and aortic tension recordings. The latter, however, are preliminary in nature.

We completely agree with the reviewer that there is ample room for further studies that could characterize different tissues important in blood pressure regulation (such as resistance arteries), elucidate even more physiological detail (such as modulatory effects of the endothelium), or look deeper into the pharmacology using chemically altered Mangostin derivatives. While we very much like this to happen in future projects, in this study we focused on the functional aspects of a-Mangostin in BK channel gating. We present our tension recordings as a proof-of-concept to underline the activity of a-Mangostin in native tissues, and we clearly show the importance of the BK channel by using iberiotoxin as a specific inhibitor which impressively abolished relaxation.

References:

Abramson, J. et al. (2024) “Accurate structure prediction of biomolecular interactions with AlphaFold 3,” Nature, 630(8016), pp. 493–500. Available at: https://doi.org/10.1038/s41586-024-07487-w.

Reviewer #2 (Public review):

Summary:

In the present manuscript, Cordeiro et al. show that α-mangostin, a xanthone obtained from the fruit of the Garcinia mangostana tree, behaves as an agonist of the BK channels. The authors arrive at this conclusion through the effect of mangostin on macroscopic and single-channel currents elicited by BK channels formed by the α subunit and α + β1 sununits, as well as αβ1 channels coexpressed with voltage-dependent Ca2+ (CaV1,2) channels. The single-channel experiments show that α-mangostin produces a robust increase in the probability of opening without affecting the single-channel conductance. The authors contend that α-mangostin activation of the BK channel is state-independent and molecular docking and mutagenesis suggest that α-mangostin binds to a site in the internal cavity. Importantly, α-mangostin (10 μM) alleviates the contracture promoted by noradrenaline. Mangostin is ineffective if the contracted muscles are pretreated with the BK toxin iberiotoxin.

Strengths:

The set of results combining electrophysiological measurements, mutagenesis, and molecular docking reveals α-mangostin as a potent activator of BK channels and the putative location of the α-mangostin binding site. Moreover, experiments conducted on aortic preparations from mice suggest that α-mangostin can aid in developing drugs to treat a myriad of diverse diseases involving the BK channel.

We thank the reviewer for pointing out the significance of our study.

Weaknesses:

Major:

(1) Although the results indicate that α-mangostin is modifying the closed-open equilibrium, the conclusion that this can be due to a stabilization of the voltage sensor in its active configuration may prove to be wrong. It is more probable that, as has been demonstrated for other activators, the α-mangostin is increasing the equilibrium constant that defines the closed-open reaction (L in the Horrigan, Aldrich allosteric gating model for BK). The paper will gain much if the authors determine the probability of opening in a wide range of voltages, to determine how the drug is affecting (or not), the channel voltage dependence, the coupling between the voltage sensor and the pore, and the closed-open equilibrium (L).

We would like to take the opportunity to clarify this potential misunderstanding. In our manuscript, we have discussed three mechanistic explanations for the Mangostin activation: (1) an electrostatic effect at the selectivity filter, (2) structural and electrostatic changes of S6 that facilitate the opening of a putative lower gate, and (3) hydrophobic gating, i.e., counteracting dewetting of the pore. All possibilities would impact S6 and lower the free energy for pore opening, and we concur that therefore Mangostin most likely affects the closed-open equilibrium (L) of the BKα channel.

The sentence at the original lines 470-471, “(…) caused by an enhanced shift of the closed-open equilibrium toward the open state, such as the stabilization of the voltage sensor in an active conformation” refers to the observation that the presence of the β1 subunit enhances this closed-open shift. The stabilization of the voltage sensor domain was mentioned as one example of how it achieves this. We recognize that this example was an unfortunate choice, as β1 rather facilitates Ca²⁺-dependent allosteric pore opening unrelated to the discussed mechanisms of Mangostin. We have therefore removed this statement.

As to the suggestion to dissect the effect of Mangostin on C, D, and L, we agree with the reviewer that this would surely add to a full biophysical characterization. However, in our project, we strove towards including more experiments showing the physiological implications of Mangostin activation to emphasize the implication for vasodilation. We hope the reviewer understands that, with limited resources, this came at the expense of a full investigation of the different gating components, which could pose a separate project by itself.

(2) Apparently, the molecular docking was performed using the truncated structure of the human BK channel. However, it is unclear which one, since the PDB ID given in the Methods (6vg3), according to what I could find, corresponds to the unliganded, inactive PTK7 kinase domain. Be as it may, the apo and Ca2+ bound structures show that there is a rotation and a displacement of the S6 transmembrane domain. Therefore, the positions of the residues I308, L312, and A316 in the closed and open configurations of the BK channel are not the same. Hence, it is expected that the strength of binding will be different whether the channel is closed or open. This point needs to be discussed.

We apologize for the typing error and thank the reviewer for indicating this erroneous PDB ID. (“6vg3”). It should have read PDB ID 6v3g as in the legend to Fig. 4B. The reviewer appropriately points out that there are differences in the S6 segment addressed in our study between the two available cryo-EM structures obtained in the presence (PDB ID 6v38) and absence of Ca²⁺ (PDB ID 6v3g) (Tao and MacKinnon, 2019).

We had actually performed the docking with both structures, but chosen to show the Ca²⁺-free structure to better visualize the I308 position. a-Mangostin is found in the same S6 region in both, not obstructing the K⁺ conduction pathway. The binding energies of the favored poses are very similar; the binding energy in the best-ranking conformational cluster in the Ca²⁺-bound structure even was slightly lower (-8.64 kcal mol^-1) than in the docking with the Ca²⁺-free channel (-8.58 kcal mol^-1; Fig. 4B), which may not be a relevant difference.

We compared the residue interactions in both dockings (Author response table 1). S317 and Y318, which did not reduce the shift in V_½ upon substitution, were not predicted to contact a-Mangostin in either structure. In both structures, L312 and F315 were predicted to interact in virtually all poses analyzed. In the docking to the Ca²⁺-free state, also I308 was predicted to interact in 17/20 poses, while contacts to A316 occurred in 5/20 poses. In the Ca²⁺-bound state, predicted interactions shifted from I308 (which is expected as it is buried in the protein) to A316, and the isoprenyl moiety close to I308 rotated downwards. This could indicate that a-Mangostin adopts a more horizontal position following the upward reorientation of S6 in the Ca²⁺-bound state when the channel moves from one to the other conformation (Fig. S4).

Author response table 1.

Number of interactions of S6 residues in 20 analyzed α-Mangostin poses in the molecular dockings to the Ca2+-free and Ca2

These docking results are consistent with our functional measurements. Recent structures of the BK/γ1 complex showed that the VSD and Ca²⁺-bowl are stabilized in an active-like conformation that corresponds to the conformation seen in the Ca²⁺-bound state (Kallure et al., 2023; Yamanouchi et al., 2023; Redhardt, Raunser and Raisch, 2024), indicating that very likely the Ca²⁺-bound and Ca²⁺-free structures indeed represent open and closed conformations of the channel. We observed that α-Mangostin can bind to both of these states to activate the channel (Fig. 3C, D), showing the presence of a binding site in both conformations. Further, α-Mangostin induced a left-shift in V_½ also in higher Ca²⁺ concentration (Fig. 2D), indicating that it still binds to and activates the channel after the conformational change in S6. As we could not determine affinity for the mutants due to limited solubility, we have no information on the nature of the contribution of the substitutions, i.e., reduced binding or allosteric effect. As I308 is buried in the Ca²⁺-bound state, its contribution is likely mostly allosteric. We have also proposed dewetting as possible activation mechanism, which we expect to be less sensitive to the exact pose of a molecule (as shown for NS11021, Nordquist et al., 2024). Therefore, α-Mangostin could, e.g., change solvent accessibility of the I308 sidechain, energetically favoring the buried (open) state.

We have now included both dockings and Author response table 1 in Fig. S4, and we have added passages to the results section (starting at line 373) and discussion section (starting at lines 544, 588).

Minor:

(1) From Figure 3A, it is apparent that the increase in Po is at the expense of the long periods (seconds) that the channel remains closed. One might suggest that α-mangostin increases the burst periods. It would be beneficial if the authors measured both closed and open dwell times to test whether α-mangostin primarily affects the burst periods.

We thank the reviewer for this valuable suggestion, which we have implemented. In our single channel measurements shown in our original Fig. 3 we have not observed burst behavior of the BKɑ channels. This can be explained by the fact that we measured in resting condition (100 nM free Ca_i</sup>2+</sup>) and with rather mild depolarisation (+40 mV) where Po was very low. We have therefore analyzed measurements in 5 µM free a_i</sup>2+</sup> where we recorded sufficient burst activity also in the basal state.

The burst analysis showed that ɑ-Mangostin indeed prolongs bursts and shortens the interburst closures. Within bursts, both closed times and open times were increased, and we recorded a higher number of opening events per burst. We conclude that ɑ-Mangostin acts in both the closed and the open state, where it slows open-closed transitions resulting in less flicker, and stabilizes the open state via longer open times and a higher probability for closed-open transitions.

We now show this data in Fig. 3D-F and Table S8, and have accordingly added passages to the results section (starting at line 285), the discussion (line 510), and the methods section (starting at line 746).

(2) In several places, the authors make similarities in the mode of action of other BK activators and α-mangostin; however, the work of Gessner et al. PNAS 2012 indicates that NS1619 and Cym04 interact with the S6/RCK linker, and Webb et al. demonstrated that GoSlo-SR-5-6 agonist activity is abolished when residues in the S4/S5 linker and in the S6C region are mutated. These findings indicate that binding of the agonist is not near the selectivity filter, as the authors' results suggest that α-mangostin binds.

We will gladly clarify our ideas concerning the binding sites of other activators and ɑ-Mangostin. We first hypothesized that ɑ-Mangostin may share characteristics and mode of action with the class of negatively charged activators (NCA) that we have described before (Schewe et al., 2019). NCA were found to occupy a common fenestration site that is located close to the selectivity filter in TREK K2P channels, and in this manuscript we have shown by THexA competition and mutagenesis experiments that ɑ-Mangostin also binds in this fenestration region in TREK-1 channels (Fig. S3).

The existence of this common NCA binding site was also proposed for BK channels, as a docking placed the NCA NS11021 in an equivalent binding region, and, among others, NS11021 and GoSlo-SR-5-6 competed with THexA for binding in the pore (Schewe et al., 2019). These results were indeed not fully in agreement with the proposed binding site of GoSlo-SR-5-6 in Webb et al. (2015), although the most effective (double) mutants were located at S317 and I323, at the intracellular end of the cleft between neighboring S6 segments. In this manuscript, we have shown that α-Mangostin is present in the pore of BK channels by molecular docking, a THexA competition assay, and two mutations that reduced the shift in V_½ induced not only by ɑ-Mangostin but also by GoSlo-SR-5-6 (Fig. 4). While the docking was rather a starting point, both functional tests argue against a binding site in the S4/5 linker/S6C region; however, allosteric mechanisms could still reduce activation also in mutants in the S4/5 linker/S6C region far from the pore binding region proposed by us in the 2019 study and the present manuscript.

To summarize, we did not mean to imply that all BK activators should bind to this site, especially if they are not part of the NCA class (as NS1619, Cym4, as well as BC5, whose different binding site enabled us to use it as a control in our THexA competition assay). However, the cleft close to gating relevant S6 residues may well pose a region especially susceptible to modulator binding (as BL-1249, GoSlo-SR-5-6, and ɑ-Mangostin). We have moved, respectively separated, the initial GoSlo references from the reference to the pore binding site in the paragraph (lines329, 358) to improve clarity.

(3) The sentence starting in line 452 states that there is a pronounced allosteric coupling between the voltage sensors and Ca2+ binding. If the authors are referring to the coupling factor E in the Horrigan-Aldrich gating model, the references cited, in particular, Sun and Horrigan, concluded that the coupling between those sensors is weak.

We are grateful for the opportunity to improve this passage. We intended to express that observed effects (in this case the shift in V_½) are pronounced around 1 µM Ca²⁺. As the reviewer states, the coupling factor between the voltage and calcium sensors (E; 2.4) is weak compared to the coupling of Ca²⁺ (C; 8) and voltage (D; 25) to the pore in the Horrigan-Aldrich model. However, the shape of the Ca²⁺-dependence of V_½ cannot be completely described when E is neglected, with the highest difference around 1-2 µM Ca²⁺ (Horrigan and Aldrich, 2002). Deletion of the gating ring underlines the allosteric sensor coupling (Clay, 2017). This together with the steep Ca²⁺-dependence in this concentration range (meaning high Po changes upon occupancy increase; Cui, Cox and Aldrich, 1997) explains the higher apparent activation, visible as the higher shift in V_½ observed at the 1 µM Ca²⁺. Speaking with the model of Sun and Horrigan (2022), the suppressing “molecular logic gate” is already relieved by the presence of intermediate Ca²⁺, and the direct “gating lever” pathway via voltage acts synergistically and achieves the observed higher V_½ shift upon depolarization. We have adapted the sentence and separated the citations for better understanding (lines 503-507).

References:

Clay, J.R. (2017) “Novel description of the large conductance Ca2+-modulated K+ channel current, BK, during an action potential from suprachiasmatic nucleus neurons,” Physiological Reports, 5(20), p. e13473. Available at: https://doi.org/10.14814/phy2.13473.

Cui, J., Cox, D.H. and Aldrich, R.W. (1997) “Intrinsic Voltage Dependence and Ca2+ Regulation of mslo Large Conductance Ca-activated K+ Channels,” Journal of General Physiology, 109(5), pp. 647–673. Available at: https://doi.org/10.1085/jgp.109.5.647.

Horrigan, F.T. and Aldrich, R.W. (2002) “Coupling between voltage sensor activation, Ca2+ binding and channel opening in large conductance (BK) potassium channels,” The Journal of General Physiology, 120(3), pp. 267–305. Available at: https://doi.org/10.1085/jgp.20028605.

Kallure, G.S. et al. (2023) “High-resolution structures illuminate key principles underlying voltage and LRRC26 regulation of Slo1 channels.” bioRxiv, p. 2023.12.20.572542. Available at: https://doi.org/10.1101/2023.12.20.572542.

Nordquist, E.B., Jia, Z., Chen, J., 2024. “Small Molecule NS11021 Promotes BK Channel Activation by Increasing Inner Pore Hydration.” J. Chem. Inf. Model. 64, 7616–7625. https://doi.org/10.1021/acs.jcim.4c01012

Redhardt, M., Raunser, S. and Raisch, T. (2024) “Cryo-EM structure of the Slo1 potassium channel with the auxiliary γ1 subunit suggests a mechanism for depolarization-independent activation,” FEBS Letters, 598(8), pp. 875–888. Available at: https://doi.org/10.1002/1873-3468.14863.

Schewe, M. et al. (2019) “A pharmacological master key mechanism that unlocks the selectivity filter gate in K + channels.,” Science, 363(6429), pp. 875–880. Available at: https://doi.org/10.1126/science.aav0569.

Sun, L. and Horrigan, F.T. (2022) “A gating lever and molecular logic gate that couple voltage and calcium sensor activation to opening in BK potassium channels,” Science Advances, 8(50), p. eabq5772. Available at: https://doi.org/10.1126/sciadv.abq5772.

Tao, X. and MacKinnon, R. (2019) “Molecular structures of the human Slo1 K+ channel in complex with β4,” eLife 8, p. e51409. Available at: https://doi.org/10.7554/eLife.51409.

Webb, T.I. et al. (2015) “Molecular mechanisms underlying the effect of the novel BK channel opener GoSlo: Involvement of the S4/S5 linker and the S6 segment,” Proceedings of the National Academy of Sciences, 112(7), pp. 2064–2069. Available at: https://doi.org/10.1073/pnas.1400555112.

Yamanouchi, D. et al. (2023) “Dual allosteric modulation of voltage and calcium sensitivities of the Slo1-LRRC channel complex,” Molecular Cell, 83(24), pp. 4555-4569.e4. Available at: https://doi.org/10.1016/j.molcel.2023.11.005.

Reviewer #3 (Public review):

Summary:

This research shows that a-mangostin, a proposed nutraceutical, with cardiovascular protective properties, could act through the activation of large conductance potassium permeable channels (BK). The authors provide convincing electrophysiological evidence that the compound binds to BK channels and induces a potent activation, increasing the magnitude of potassium currents. Since these channels are important modulators of the membrane potential of smooth muscle in vascular tissue, this activation leads to muscle relaxation, possibly explaining cardiovascular protective effects.

Strengths:

The authors present evidence based on several lines of experiments that a-mangostin is a potent activator of BK channels. The quality of the experiments and the analysis is high and represents an appropriate level of analysis. This research is timely and provides a basis to understand the physiological effects of natural compounds with proposed cardio-protective effects.

We sincerely thank the reviewer for appraising the achievements of our study.

Weaknesses:

The identification of the binding site is not the strongest point of the manuscript. The authors show that the binding site is probably located in the hydrophobic cavity of the pore and show that point mutations reduce the magnitude of the negative voltage shift of activation produced by a-mangostin. However, these experiments do not demonstrate binding to these sites, and could be explained by allosteric effects on gating induced by the mutations themselves.

We are aware that our functional data are unfortunately not sufficient to clearly distinguish between effects due to affinity loss or due to allosteric mechanisms. Our attempts to generate complete dose–response curves for the mutants to determine accurate apparent IC₅₀ values were unfortunately limited by the solubility of the compound. Consequently, we have avoided making claims about affinity loss in the mutant analysis, and have instead only reported the reduction in potency, expressed as the shift in V_½. To reduce confounding effects from the mutations themselves, we selected substitutions that preserved the most wildtype-like GV-relationships, based on the extensive mutagenesis work of (Chen, Yan and Aldrich, 2014). We address this matter also in our answer to Recommendation (6) below, and we have replaced the word “binding” in the title of the manuscript. Nevertheless, we consider the proposed binding region to be well supported by the THexA competition experiments in combination with molecular docking, even though the specific mechanistic contributions of individual residues cannot yet be resolved.

Reviewer #3 (Recommendations for the authors):

(1) Natural xanthones as α-Mangostin induce vasorelaxation via binding to key gating residues in the S6 domain of BK channels.

(2) If α-Mangostin occupies a similar binding site to quaternary ammoniums, what is the explanation for not observing a reduction in the single-channel current (fast blocking effect)? The α-Mangostin site proposed here is in a region of the channel that should occlude ion permeation. The authors should discuss possible explanations for this apparently contradictory observation.

As the reviewer states, we indeed have not observed a reduced single channel amplitude in any measurement. The THexA competition assay showed that ɑ-Mangostin is present in the pore cavity and interferes with THexA access to its binding site. However, we do not think that their binding sites are similar, as QA ions bind directly below the filter entrance to block permeation, while our studies suggest that ɑ-Mangostin binds in the upper portion of the cleft between S6 helices. In this position, it would clearly overlap with the QA binding site and hinder access, but not block permeation. We would therefore not expect to see an amplitude reduction by intermittent α-Mangostin block. Consistently, all binding poses in our dockings were close to the cavity wall, without interfering with the central ion conduction pathway. To better illustrate this, we have added updated intracellular views of the dockings in the Ca²⁺-free and Ca²⁺-bound state (which we have also now included as suggested by another reviewer) to the supplementary information (Fig. S4A).

(3) In Figure 2D, it is difficult to appreciate the differences between the symbols representing the G-V relationships of BKa channels at different intracellular Ca concentrations, before and after activation with 10 μM a-Mangostin. A clearer distinction between the curves would help to interpret the data more easily.

We thank the reviewer for the suggestion to improve figure accessibility. We have changed the line appearance for better discrimination of the overlying portions.

(4) Both THexA and TPA block BK channels through voltage and state-dependent mechanisms. Therefore, their apparent affinity could change if a-Mangostin simply increases open probability or alters dwell times rather than physically blocking access to the binding site.

The reviewer addresses valid limitations that can affect the meaningfulness of competition experiments under certain conditions. However, we think that this does not apply to our results:

Previous studies have shown that the voltage dependence of quaternary ammonium blockers up to C₁₀ is rather weak in BK channels, and only a slight increase in block is present in the voltage range +30 mV to +100 mV (Li and Aldrich, 2004; Thompson and Begenisich, 2012). Hence, THexA voltage dependence has already reached a plateau in the competition assay (at +40 mV), and its voltage dependence would have little effect on our results.

Controversy exists about the nature of the state dependence of different quaternary ammonium blockers, but TBA is often recognized as an open channel blocker of BK channels, which probably also applies to THexA (Wilkens and Aldrich, 2006; Tang, Zeng and Lingle, 2009; Thompson and Begenisich, 2012; Posson, McCoy and Nimigean, 2013). Assuming such an open-channel block, apparent IC₅₀ values would be inversely proportional to Po. The THexA IC₅₀ was about 80 nM in the basal state, when Po is very low (0.024 at +40 mV as derived from the GV-relationship); an increase of open dwell times, respectively Po, in the presence of α-Mangostin to, e.g., 0.3 would therefore lead to a ≈10-fold decrease in apparent IC₅₀. However, the apparent THexA IC₅₀ strongly increased rather than decreased (more than 20-fold to around 1.6 µM). This cannot arise from Po change and must reflect the altered access of THexA to its binding site caused by α-Mangostin. Assuming a pure closed channel block where apparent IC₅₀ would correlate with the closed times, an increase of about 1.4-fold is expected. However, we recorded a much stronger 20-fold increase. Therefore, we are convinced that we have conclusively shown that α-Mangostin is present in the BK pore irrespective of the state dependence of THexA block.

(5) The pH dependence of the V1/2 shift supports the idea that α-Mangostin becomes more negatively charged at higher pH (enhancing its effect.) However, although the data are consistent with this interpretation, additional controls such as using a non-ionizable analog or assessing solubility changes with pH would be needed to confirm that the shift is caused specifically by ionization of α-Mangostin and not by indirect pH effects on channel gating.

We agree with the reviewer that the pH experiment by itself is not sufficient to clearly tie the existence of a charge to a possible activation mechanism. We still think that this is an interesting observation and should be made known, as we have investigated the mechanism of negatively charged activators in different K⁺ channel families before (Schewe et al., 2019). Unfortunately, we do not have access to uncharged derivatives mimicking the 3D conformation. From the commercially available substances, the bare xanthone backbone is completely insoluble in water. We have therefore tested the derivative 3-hydroxyxanthone as example with a minimal number of hydroxyl substituents (Author response image 2, Author response table 2 ). The 3-hydroxyxanthone indeed shows reduced activation compared to α-Mangostin. The shift in V_½ induced by 10 µM 3-hydroxyxanthone was only 14.99 ± 5.67 mV (≈50 mV for α-Mangostin). This supports that the presence of several (potentially) charged substituents is important for the activation mechanism. However, we have no knowledge about the efficacy of the compound or the local pK_a of the different hydroxyl groups. As the reviewer stated, systematic chemical modifications would be necessary to elucidate the importance of the charged substituent number and positions, which is not within our capabilities.

Author response image 2.

Activation of BKα by 3-hydroxyxanthone. (A) GV-relationship before and after application of 10 µM 3-hydroxyxanthone. (B) V_½ before and after application of 10 µM 3-hydroxyxanthone compared to α-Mangostin and the resulting difference in V_½ (ΔV_½). Measurements were conducted as described in the main manuscript with 100 nM free Ca_i²⁺.

Author response table 2.

Comparison of the V_½ ± SEM and ΔV_½ ± SEM before and after activation by 10 µM α-Mangostin or 10 µM 3-hydroxyxanthone in BKα channels. Unpaired t-test, two-tailed P values (α=0.05)

(6) The reduced V1/2 shifts observed in the I308A, L312M, and A316PP mutants may result from intrinsic gating alterations rather than a true loss of a-Mangostin binding. The GoSlo-SR-5-6 control is informative, but the persistence of activation in A316P does not fully resolve this. A more convincing test would be employing double or triple mutants.

As stated above, we acknowledge that our functional data do not allow us to definitively separate effects arising from a true loss of binding affinity from those due to potential allosteric effects. We tried to minimize intrinsic gating alteration brought by substitutions by not conducting a pure alanine or cysteine scanning mutagenesis. Instead, substitutions were chosen to be closest to the wildtype GV-relationship in (Chen, Yan and Aldrich, 2014) where possible. While L312M was virtually identical to the wildtype, A316P showed a change in slope in high Ca²⁺ concentrations, which could indicate a changed voltage sensitivity. Additionally, A316P completely abolished α-mangostin activation. We therefore also used A316G to ensure that the channel is functional and retains voltage sensitivity, even if its V_½ was shifted stronger. As we have conducted paired measurements and assessed the V_½ before and after activation, we are confident that we can attribute a reduced shift to the reduced action of α-mangostin.

Following the reviewer’s suggestion, we have generated and measured the double mutants I308A/L312M, I308A/A316G, and L312M/A316G (the triple mutant I308A/L312M/A316G did not produce measurable currents). The mutants I308A/L312M and I308A/A316G showed a moderate energy-additive effect and reduced the shift in V_½ by further ≈7 mV compared to the single mutation with the stronger shift. The combination L312M/A316G, however, did not further reduce the shift seen in the single mutations and did not even produce the shift induced by A316G alone.

Author response image 3.

Double Mutants I308A/L312M, I308A/A316G and L312M/A316G compared to the single mutations in the main manuscript. The V½ before and after activation with 10 µM α-Mangostin, the resulting shift in V½, and the GV-relationships are shown (n=6-7), measurements were made as in Fig. 4.

Author response table 3.

Summary of the V_½ before and after Mangostin activation and the resulting shifts in V_½ for the double mutants compared to the single mutants shown in the main manuscript.

Following a suggestion by another reviewer, we have generated Alphafold3 (AF3) models for I308A, L312M and A316P and repeated the Mangostin docking. We learned that the mutations are all predicted to substantially impact the structure of the S6 helix, therefore altering the binding region, and A316P especially impacted the nature of residue interactions. This could be an explanation why the double mutants do not show a clear and consistent additive effect.

Unfortunately, this outcome is not conclusive and the double mutants do not reveal further information compared to the single mutants. We have therefore decided not to include these measurements in the manuscript.

As we do not know if our answers will be sent to all reviewers, we repeat the relevant part about the AF3 models here:

(…) According to these predictive models,

The I308A substitution considerably straightens the S6 helix starting at this residue. Hence, all residues are displaced relative to the WT: C_a of L312, F315, and A316 are displaced by 2.8 Å, 4.2 Å, and 4.6 Å, respectively, widening the bottom of the binding pocket. However, the prediction confidence is rated lower as in the other AF3 models for all helices (70 > plDDT > 50). In the docking, poses in the binding pocket comparable to these observed in the WT (i.e. involving I308A, L312 and A316) and with the same molecule orientation have higher binding energies (-7.13 to -6.66 kcal mol^-1). Additionally, poses without contact to I308A arise that have a more vertical position, indicating that the structural change affects the binding region.

The changes induced by L312M are localized to residues 313-323, where S6 bends towards S5. Binding energies are lower especially in the best 2 poses that are also most comparable to the WT docking (-9.88 kcal mol^-1), but clustering overall is poor and poses are more heterogeneous. Interactions with L312M are completely abolished, while interactions with I308 (in 11/20 poses), F315 (in all poses), and A316 (in 5/20 poses) persist. Because of the rather small structural alteration induced by the substitution and the variable poses one could speculate that the reduced V_½ shift is due to the observed loss in binding to L312M; however, retained interactions to the other residues would still allow α-Mangostin to activate.

A316P induces a displacement of the S6 helix compared to the WT while the other pore helices are not affected. S6 shows an enhanced outward bending around A316, which results in displacements of residues where a-Mangostin would bind, i.e., the C_a of F315 and L312M are displaced by 2.4 Å and 2.8 Å (I308 is not affected). Residues below are moved in a more rotational way, resulting in a C_a displacement of 3.1 Å for Y318 and even 5.7 Å for V319, before displacements decrease again towards the intracellular helix end. While interactions with A316P are present in 10/20 analyzed poses, the helix displacement seems to hinder I308 and L312 interactions, as the best docked a-Mangostin pose (-8.41 kcal mol^-1) is predicted to only contact F315 and Y318, and overall, any I308 or L312 contacts only occurred in 3/20 and 7/20 poses (wildtype: 17/20 and 20/20 poses). This may hint at a mechanism where A316P probably has a substantial allosteric share in reducing the V_½ shift induced by a-Mangostin and underlines the exceptional effect of this mutation (i.e., complete loss of a V_½ shift). (…)

(7) The subtraction approach used to isolate BK currents (difference before and after a-Mangostin) assumes that the compound affects only BK channels. However, a-Mangostin could also modulate Cav currents directly, as reported for other polyphenolic compounds. No vehicle (DMSO) control is shown.

We agree with the reviewer that α-Mangostin could also modulate Ca_v currents; however, this would not interfere with the conclusions drawn from this nanodomain experiment. We intended to show the overall current modulation by ɑ-Mangostin in the voltage range relevant for Ca_v-BK coupling, as this would be the determinant for the membrane potential mediating the vasoactive effect. In native tissue, BK and Ca_v channels (among others) would likewise contribute to the net membrane conductance, with BK channels being a major contributor when activated. In fact, a concomitant inhibition of Ca_v channels could act synergistically in favor of vasodilation. This could therefore be a subject for the further investigation of potential ɑ-Mangostin targets. However, the fact that iberiotoxin prevented relaxation in aortic preparations conclusively showed that BK channels are the major player in native tissue.

We have reformulated some sentences to prevent misunderstandings that we refer to isolated BK currents instead of α-Mangostin activated currents.

DMSO controls were conducted and did not impact BK or Ca_v1.2 currents or the aortic tissue contraction. We have added representative measurements as Fig. S6 and stated the DMSO concentration in the Methods section (line 655).

(8) Most kinetic fits were obtained at strong depolarizations (around +100 mV), which limits how well these results can be extrapolated to physiological voltages. Although the BK-Cav experiments show facilitation between -50 and +50 mV, providing plots for activation and deactivation in that range would strengthen the physiological relevance.

We thank the reviewer for this valuable suggestion. We now additionally show that the impact of ɑ-Mangostin on activation is high at lower depolarisation, indeed underlining its physiological relevance. To address the activation time course in a more physiological voltage range, we have used our measurements of BKɑ channels in 10 µM Ca_i</sup>2+</sup> (where the V_½ shift induced by ɑ-Mangostin is equal to 100 nM ca_i²⁺+; Fig. 2D). The outward currents already present in the lower voltage range under these conditions allowed us to fit a monoexponential function to the traces of 0 mV to 100 mV prepulses. The τ of activation decreased from 29.6 ± 3.1 ms at 0 mV to 2.4 ± 2 ms at +100 mV. After ɑ-Mangostin activation, the time course was accelerated, with a τ of activation of 9.5 ± 4.7 ms at 0 mV to 2 ± 0.6 ms at +100 mV. This faster activation was particularly effective in the lower voltage range far from high Po, e.g., ɑ-Mangostin caused a decrease of more than half of the τ of activation at +20 mV (from 12.2 ± 0.6 ms to 4.98 ± 1.6 ms).

Our data consists of families of different prepulse voltages and a fixed repolarisation step (to -50 mV for 100 nM free Ca_i²⁺, and to -100 mV for 10 µM free Ca_i²⁺). Thus, we are not able to add plots for the voltage-dependence of deactivation in the same way as for activation. However, we can present the deactivation time constants of lower prepulse voltage steps that produce outward currents in symmetrical ion conditions with 10 µM free Ca_i</sup>2+</sup>. For -20 mV and +20 mV prepulse voltages, which better reflect physiological depolarisation, the deactivation time constant shows a 3-to 5-fold increase after ɑ-Mangostin activation.

We now show the plot for the voltage dependence of activation in Fig. S2A and a bar graph for activation/ deactivation time constants at +20 mV as Fig. S2B; data are summarized in Table S5. We hope this adds to illustrating the effect of ɑ-Mangostin under physiological conditions.

(9) Minor: In several parts of the paper, induced shifts to negative voltages are referred to "leftward shifts". It would be useful to be consistent and employ a more specific reference to negative or positive directions.

We thank the reviewer for the careful reading and have harmonized the terminology.

References

Chen, X., Yan, J. and Aldrich, R.W. (2014) “BK channel opening involves side-chain reorientation of multiple deep-pore residues,” Proceedings of the National Academy of Sciences, 111(1), pp. E79–E88. Available at: https://doi.org/10.1073/pnas.1321697111.

Li, W. and Aldrich, R.W. (2004) “Unique Inner Pore Properties of BK Channels Revealed by Quaternary Ammonium Block,” Journal of General Physiology, 124(1), pp. 43–57. Available at: https://doi.org/10.1085/jgp.200409067.

Posson, D.J., McCoy, J.G. and Nimigean, C.M. (2013) “The voltage-dependent gate in MthK potassium channels is located at the selectivity filter,” Nature Structural & Molecular Biology, 20(2), pp. 159–166. Available at: https://doi.org/10.1038/nsmb.2473.

Schewe, M. et al. (2019) “A pharmacological master key mechanism that unlocks the selectivity filter gate in K + channels.,” Science, 363(6429), pp. 875–880. Available at: https://doi.org/10.1126/science.aav0569.

Tang, Q.-Y., Zeng, X.-H. and Lingle, C.J. (2009) “Closed-channel block of BK potassium channels by bbTBA requires partial activation,” The Journal of General Physiology, 134(5), pp. 409–436. Available at: https://doi.org/10.1085/jgp.200910251.

Thompson, J. and Begenisich, T. (2012) “Selectivity filter gating in large-conductance Ca2+-activated K+ channels,” Journal of General Physiology, 139(3), pp. 235–244. Available at: https://doi.org/10.1085/jgp.201110748.

Wilkens, C.M. and Aldrich, R.W. (2006) “State-independent block of BK channels by an intracellular quaternary ammonium.,” The Journal of General Physiology, 128(3), pp. 347–364. Available at: https://doi.org/10.1085/jgp.200609579.

Author Response:

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

We thank the reviewers and editors for their careful reading of our manuscript and thoughtful comments on it. We appreciate the overall positive opinion on our manuscript and helpful comments and suggestions from the reviewers. Overall, the main points identified by reviewers were 1) further broadening of the system to a range of inputs as well as the construct types that can be generated with the system and 2) Further consideration of any off-target joining or off-target effects on genes/proteins and the limits to the expandability of the kit. To address these concerns, we have added new data in Figure 6, illustrating the generation of a new construct using PCR and dsDNA fragments, new constructs for mpeg1.1 and for CRISPR gRNA expression and have revised the text to further address concerns and limitations of the toolkit. We thank the reviewers and editors for these suggestions and feel that they have substantially improved the manuscript.

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors introduce ImPaqT, a modular toolkit for zebrafish transgenesis, utilizing the Golden Gate cloning approach with the rare-cutting enzyme PaqCI. The toolkit is designed to streamline the construction of transgenes with broad applications, particularly for immunological studies. By providing a versatile platform, the study aims to address limitations in generating plasmids for zebrafish transgenesis.

Strengths:

The ImPaqT toolkit offers a modular method for constructing transgenes tailored to specific research needs. By employing Golden Gate cloning, the system simplifies the assembly process, allowing seamless integration of multiple genetic elements while maintaining scalability for complex designs. The toolkit's utility is evident from its inclusion of a diverse range of promoters, genetic tools, and fluorescent markers, which cater to both immunological and general zebrafish research needs. Furthermore, the modular design ensures expandability, enabling researchers to customize constructs for diverse experimental designs. The validation provided in the manuscript is solid, demonstrating the successful generation of several functional transgenic lines. These examples highlight the toolkit's efficacy, particularly for immune-focused applications.

We appreciate the overall positive evaluation of our toolkit and the time and effort in evaluating it.

Weaknesses:

While the toolkit's technical capabilities are well-demonstrated, there are several areas where additional validation and examples could enhance its impact. One limitation is the lack of data showing whether the toolkit can be directly used for rapid cloning and testing of enhancers or promoters, particularly cloning them directly from PCR using PaqCI overhangs without needing an entry vector. Similarly, the feasibility of cloning genes directly from PCR products into the system is not demonstrated, which would significantly increase the utility for researchers working with genomic elements.

This is an excellent point. Given the increased use of gene synthesis and dsDNA fragments, we also thought it was good to demonstrate incorporation of these as well. We have added a new figure, Figure 6, which demonstrates generation of two new transgene constructs constructed by direct cloning of three PCR products along with a synthetic dsDNA fragment into a Tol2 flanked backbone plasmid as an alternative, rapid approach to generation of transgenes. The resulting plasmids, encoding the mpeg1.1. promoter, a separate p2a, and a tdTomato fluorescent protein along with either wildtype or dominant negative rac2 were properly assembled and in transient transgenic zebrafish injected with these constructs, dominant negative rac2 prevented macrophage recruitment to tail wounds, indicating that this approach worked for the generation of functional transgenes. These results are discussed in new text (lines 304-391) describing this new experiment and the finding that both PCR products and synthesized dsDNA could be efficiently incorporated in constructions generated with our approach as well as in the discussion (lines 494-499).

The authors discuss potential applications such as using the toolkit for tissue-specific knockout applications by assembling CRISPR/Cas9 gRNA constructs. However, they do not demonstrate the cloning of short fragments, such as gRNA sequences downstream of a U6 promoter, which would be an important proof-of-concept to validate these applications. Furthermore, while the manuscript focuses on macrophage-specific promoters, the widely used mpeg1.1 promoter is not included or tested, which limits the toolkit's appeal for researchers studying macrophages and microglia.

Yes, in the new figure described above, we have now shown that this method works with shorter PCR fragments such as the p2a fragment cloned within the tdTomato-p2a-rac2 constructs described above. This fragment is ~70 bp and while this is somewhat longer than a simple gRNA targeting sequence (though smaller than a complete sgRNA), we believe that this indicates that smaller size fragments can still be incorporated within these constructs. We also agree with the general idea of increasing functionality to incorporate CRISPR/Cas9 and now include a 3E encoding the zebrafish U6 promoter. As CRISPR expression constructs frequently incorporate complex construction, for instance, expression of tagged Cas9 along with the U6 driven gRNA as in Zhou et al., 2018 or along with rescue constructs as in Wang et al., 2021, we have given these constructs the non-standard 5’ end O3c, to enable multiplexing in these complex constructs.

We agree that it is important to include mpeg1.1, given the broad use of this promoter within the field, we’ve now included an 5E mpeg1.1 construct within the toolkit.

Another potential limitation is the handling of sequences containing PaqCI recognition sites. Although the authors discuss domestication to remove these sites, a demonstration of cloning strategies for such cases or alternative methods to address these challenges would provide practical guidance for users.

Absolutely, we have now included a new figure (Supplementary Figure 6) that illustrates one domestication approach using PCR and homology-based cloning as an easy approach to domestication. In addition, we have also mentioned alternative approaches for domestication in the discussion (lines 439-444).

Reviewer #2 (Public review):

Summary:

Hurst et al. developed a new Tol2-based transgenesis system ImPaqT, an Immunological toolkit for PaqCl-based Golden Gate Assembly of Tol2 Transgenes, to facilitate the production of transgenic zebrafish lines. This Golden Gate assembly-based approach relies on only a short 4-base pair overhang sequence in their final construct, and the insertion construct and backbone vector can be assembled in a single-tube reaction using PaqCl and ligase. This approach can also be expandable by introducing new overhang sequences while maintaining compatibility with existing ImPaqT constructs, allowing users to add fragments as needed.

Strengths:

The generation of several lines of transgenic zebrafish for the immunologic study demonstrates the feasibility of the ImPaqT in vivo. The lineage tracing of macrophages by LPS injection shows this approach's functionality, validating its usage in vivo.

We appreciate the positive sentiments for our toolkit and the effort put into reviewing our manuscript.

Weaknesses:

(1) There is no quantitative data analysis showing the percentage of off-target based on these 4bp overhang sequences.

While we agree that this is an important variable for the method, we feel that previous studies that have broadly tested off-target effects of all potential 4 bp overhang sequences have already given an effective overview of interactions between each of these overhangs (Potapov et al., 2018; Pryor et al., 2020). The results from these studies were incorporated into the NEB ligase fidelity viewer that we used to predict the overhangs that would have minimal off-target with each other: the tool also reports the expected off-target ligation of individual 4 bp overhangs. In all cases, we selected overhangs that would have minimal off-target efficiency, with each of the overhangs showing 1% or less off-target ligation with any of the other overhangs chosen. We have added new text, lines 119-124, that further clarifies that our selection for these ends.

(2) There is no statement for the upper limitation of the expandability.

Yes, we’ve been curious as well. While our cloning of 6 distinct fragments in Figure 5 and a new 5 fragment cloning added in revision seen in Figure 6, suggests that 5-6 fragments can be readily assembled, in the course of revisions we also attempted to generate a larger product of 11 fragments that ultimately failed. While the 11 fragment construct was unsuccessful, it is unclear whether this is due to the constructs chosen, the potential size of the plasmid or due to a failure of the technique/enzymes themselves. Given that published descriptions of PaqCI Golden Gate cloning approaches have found that PaqCI can assemble at least 32 fragments and can produce large sequences (e.g. in Sikkema et al., 2023, where they assemble the ~40 kbp T7 genome from 12, 24 and 32 distinct fragments using a PaqCI Golden Gate reaction), we suspect that our issues with the 11 fragment assembly are likely due to complications with the specific group of constructs that were combined, however, we have not been able to exhaustively test a range of constructs and assemblies of varying complexity levels. To recognize this, we have added additional text (lines 490-493) to the discussion describing that we have only combined 6 constructs, but that we think that this likely encompasses many of the applications that may be needed for this system, while recognizing that expansion beyond this number may be possible.

(3) There is no data about any potential side effect on their endogenous function of promoter/protein of interest with the ImPaqT method.

Absolutely, we have added new text (lines 457-470) to our discussion describing the potential side effects on protein function. For instance, the need to be aware of whether N- or C-termini of proteins can be modified and recognition of the potential for affecting/creating ectopic transcription factor binding sites as potential pitfalls to keep in mind.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

The data presented in the manuscript is robust and well-supported. However, to fully demonstrate the broad applicability of the toolkit and strengthen its impact, a few additional experiments could be beneficial. Specific suggestions for these experiments and areas of improvement are outlined in the 'Weaknesses' section of the Public Review. Additionally, Figures 2-4 illustrate the same concept - cloning three fragments from entry vectors-which comes across as repetitive. Incorporating a more diverse range of use cases would better highlight the versatility of the toolkit.

As we described in our replies to your public points above, we have now added new Figure 6 and new Supplementary Figure 6 addressing the cloning of PCR fragments, short fragments as well as a mechanism of domestication. We have also included the mpeg1.1 promoter within the toolkit. In addition, your point on the repetition of assay is fair and in our new Figure 6, we instead used wild type and dominant-negative Rac2 expression and failure of macrophage recruitment to the tail wound.

Reviewer #2 (Recommendations for the authors):

Hurst et al. developed a new Tol2-based transgenesis system ImPaqT, it is interesting and potentially efficient, but I have a few concerns:

(1) The author claimed that the ImPaqT system is more efficient than other existing systems. The authors should provide such data to support their claim.

Our argument wouldn’t be that the ImPaqT system is strictly speaking more efficient, but rather that the combination of minimal added sequence, the ability to expand or contract the fragments used, and, in our new Figure 6, the ability to directly utilize PCR products and dsDNA fragments, while retaining the ability to combinatorially build constructs from a suite of existing sequences is the main point of the method. We now explicitly state that Golden Gate cloning isn’t more efficient than existing techniques in the text (lines 534-537), but rather the particular strength of the method is the flexibility and minimal added sequence.

(2) The ImPaqT is theoretically less prone to have off-target effects than existing systems, the authors should provide such data to validate their claim.

Good point, we have now searched the zebrafish genome for PaqCI sites as well as for BsaI and BsmBI which are the 6-base cutters most commonly used for Golden Gate cloning. We found that PaqCI cuts every ~17 kb in the zebrafish genome while BsaI and BsmBI cut every ~9 kb or ~13 kb respectively, further supporting that PaqCI sites are rarer in the genome and should generally require domestication less often. We have now added new text describing this in lines 129-132.

(3) The authors should mention any potential side effects of this system on the endogenous function of the promoter/protein of interest, at least in their discussion part.

Yes, this should absolutely be expanded, as we said in your public comments above, we have now added new text describing potential pitfalls that this method may have on promoter or gene expression.

(4) The authors are suggested to provide a balanced discussion about the expandable usage of this system beyond the immune system.

We agree, this is also a good point that we should have emphasized more. We’ve added new text (lines 537-541) recognizing that in principle, many of the components we’ve derived should be useful in non-immune systems, but we also recognize that adapting this to new tissues will require the development of new promoters within the Golden Gate system which can be combined with these already developed tools.

References

Potapov, V., Ong, J.L., Kucera, R.B., Langhorst, B.W., Bilotti, K., Pryor, J.M., Cantor, E.J., Canton, B., Knight, T.F., Evans, T.C., Jr., et al. (2018). Comprehensive Profiling of Four Base Overhang Ligation Fidelity by T4 DNA Ligase and Application to DNA Assembly. ACS Synth Biol 7, 2665-2674.

Pryor, J.M., Potapov, V., Kucera, R.B., Bilotti, K., Cantor, E.J., and Lohman, G.J.S. (2020). Enabling one-pot Golden Gate assemblies of unprecedented complexity using data-optimized assembly design. PLoS One 15, e0238592.

Sikkema, A.P., Tabatabaei, S.K., Lee, Y.J., Lund, S., and Lohman, G.J.S. (2023). High-Complexity One-Pot Golden Gate Assembly. Curr Protoc 3, e882.

Wang, Y., Hsu, A.Y., Walton, E.M., Park, S.J., Syahirah, R., Wang, T., Zhou, W., Ding, C., Lemke, A.P., Zhang, G., et al. (2021). A robust and flexible CRISPR/Cas9-based system for neutrophilspecific gene inactivation in zebrafish. J Cell Sci 134.

Zhou, W., Cao, L., Jeffries, J., Zhu, X., Staiger, C.J., and Deng, Q. (2018). Neutrophil-specific knockout demonstrates a role for mitochondria in regulating neutrophil motility in zebrafish. Dis Model Mech 11.

Author Response:

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

Public Reviews:

Reviewer #1 (Public review):

Weaknesses:

(1) The main weakness of this paper, in my view, is that it felt disconnected from the larger body of work on fitness and genotype-phenotype landscapes, including previous data on TFBSs in E. coli, genotype-phenotype maps of TFBSs in other systems, protein sequence landscapes (e.g., from mutational scans or combinatorially-complete libraries), and fitness landscapes of genomic mutations (e.g., combinatorially-complete landscapes of antibiotic resistance alleles). I have no doubt the authors are experts in this literature, and they probably cite most of it already given the enormous number of references. But they don't systematically introduce and summarize what was already known from all that work, and how their present study builds on it, in the Abstract and Introduction, which left me wondering for most of the paper why this project was necessary. Eventually, the authors do address most of these points, but not until the end, in the Discussion. Readers who have no familiarity with this literature might read this paper thinking that it's the first paper ever to study topography and evolutionary paths on genotype-phenotype landscapes, which is not true.

There were two points that made this especially confusing for me. First, in order to choose which nucleotides in the binding sites to vary, the authors invoke existing data on the diversity of these sequences (position-weight matrices from RegulonDB). But since those PWMs can imply a genotype-phenotype map themselves, an obvious question I think the authors needed to have answered right away in the Introduction is why it is insufficient for their question. They only make a brief remark much later in the Results that the PWM data is just observed sequence diversity and doesn't directly reflect the regulation strength of every possible TFBS sequence. But that is too subtle in my opinion, and such a critical motivation for their study that it should be a major point in the Introduction.

The second point where the lack of motivation in the Introduction created confusion for me was that they report enormous levels of sign epistasis in their data, to the point where these landscapes look like random uncorrelated landscapes. That was really surprising to me since it contrasts with other empirical landscape data I'm familiar with. It was only in the Discussion that I found some significant explanation of this - namely that this could be a difference between prokaryotic TFBSs, as this paper studies, and the eukaryotic TFBSs that have been the focus of many (almost all?) previous work. If that is in fact the case - that almost all previous studies have focused on eukaryotic TFBSs or other kinds of landscapes, and this is the first to do a systematic test of prokaryotic TFBS, then that should be a clear point made in the Abstract and Introduction. (I find a comparable statement only in the very last paragraph of the Discussion.) If that's the case, then I would also find that point to be a much stronger, more specific conclusion of this paper to emphasize than the more general result of observing epistasis and contingency (as is currently emphasized in the Abstract), which has been discussed in tons of other papers. This raises all sorts of exciting questions for future studies - why do the landscapes of prokaryotic TFBSs differ so dramatically from almost all the other landscapes we've observed in biology? What does that mean for the evolutionary dynamics of these different systems?

We thank the reviewer for this thoughtful and detailed critique. We agree that the original version of the manuscript did not sufficiently motivate the study early on, nor did it clearly position our work within the broader literature on genotype–phenotype (GP) and fitness landscapes. We also agree that two specific issues, the role of PWMs and the unexpectedly high levels of sign epistasis, were insufficiently explained early on, which could lead to confusion for readers not already familiar with this field.

Positioning within the broader landscape literature

In response, we have substantially revised the Abstract and Introduction to explicitly situate our work within existing empirical studies of GP and fitness landscapes, including TFBS landscapes in bacteria, eukaryotic TFBS genotype–phenotype maps, in vitro TF–DNA binding studies, deep mutational scans of proteins, and combinatorially complete fitness landscapes such as antibiotic resistance alleles (Abstract; Introduction, lines 64–85). We now make clear that our study builds directly on this extensive body of work, rather than introducing the landscape framework itself. For example, we write in the introduction:

“Over the last decade, genotype–phenotype (GP) maps and fitness landscapes have become central tools for understanding how molecular systems evolve under mutation and selection[22–25]. Such maps and landscapes have been experimentally studied for DNA[6,8,18,19,26,27], protein[28–32] and RNA[33–35] molecules, revealing key topographical properties that shape evolutionary outcomes, including epistasis[24,36]—the non-additive effects of multiple mutations on phenotype—landscape ruggedness, reflected in the number and distribution of fitness peaks, and constraints on adaptive evolution.”

At the same time, we clarify what remains rare in the literature: large-scale, in vivo genotype–phenotype landscapes for bacterial transcription factor binding sites that are sufficiently dense to support explicit evolutionary analyses. While numerous high-throughput studies have characterized bacterial regulatory elements, these datasets typically do not provide quantitative regulatory phenotypes across large genotype spaces, nor do they analyze evolutionary accessibility. To our knowledge, only one such in vivo TFBS landscape had previously been characterized at comparable resolution for a bacterial local regulator (TetR). Our work extends this approach to three global regulators, enabling systematic comparisons across prokaryotic systems (Abstract, Introduction, lines 64–85). For example, we write in the introduction:

“For transcription factor binding sites, most pertinent large-scale studies are based on in vitro binding assays, such as protein-binding microarrays (PBMs), and they focus predominantly on eukaryotic transcription factors[6]. While these studies have been instrumental in characterizing transcription factor binding preferences, they typically do not measure regulatory output in a native cellular context. In contrast, comprehensive in vivo data for bacterial TFBSs remain extremely rare. To our knowledge, only two high-resolutionin vivo landscapes have been previously mapped for bacterial regulators, those of the local regulators TetR[18] and LacI[27]. As a result, it remains unclear whether principles inferred from protein landscapes, eukaryotic TFBSs, or in vitro binding assays generalize to transcriptional regulation in bacteria, particularly for global regulators[11] that integrate multiple physiological signals.”

Why PWMs are insufficient for our question.

We agree with the reviewer that our original explanation of the role of PWMs was too cursory and should have been addressed explicitly in the Introduction. We have now revised the Introduction to clearly explain why PWMs derived from RegulonDB cannot substitute for empirical GP landscapes in our study (Introduction, lines 102–113).

In this passage we now explain that, first, PWMs are inferred from a limited number of naturally occurring binding sites—typically on the order of hundreds of sequences—whose diversity reflects evolutionary history and genomic context rather than systematic exploration of sequence space. As a result, PWMs sample only a small and biased subset of the possible TFBS variants, whereas our libraries probe tens of thousands of sequences in a controlled manner, providing substantially broader and more uniform coverage of genotype space (Introduction, lines 102–113).

Second, PWM scores are not direct measurements of regulatory strength. Instead, they represent probabilistic or heuristic scores that are primarily used for identifying candidate binding sites in genomes. Numerous studies have shown that PWM scores often correlate weakly with in vivo binding affinity or regulatory output, where DNA shape, cooperative interactions, and chromosomal context play important roles. As such, PWMs do not provide quantitative genotype–phenotype relationships for regulation strength (Introduction, lines 102–113).

Third, PWMs assume independent and additive contributions of individual nucleotide positions. This assumption excludes epistatic interactions by construction. Because epistasis is central to landscape ruggedness, peak structure, and evolutionary accessibility, PWM-based models are fundamentally unsuited to address the evolutionary questions we study here (Introduction, lines 102–113). We now explicitly state this limitation early in the manuscript, rather than only alluding to it later in the Results.

Sign epistasis and contrast with prior TFBS landscapes.

We also agree with the reviewer that the extensive sign epistasis we observe—approaching levels expected for uncorrelated random landscapes—is surprising in light of much of the existing empirical landscape literature. Importantly, as the reviewer notes, most previous TFBS landscape studies have focused on in vitro binding systems or on eukaryotic transcription factors, which tend to exhibit smoother and more additive landscapes.

To address this concern, we have revised the Abstract and Introduction to explicitly frame this contrast as a central result of the study (Abstract; Introduction, lines 151-153, Discussion, lines 652–668). For example, we write in the discussion:

“We showed that the regulatory landscapes of all three TFs are highly rugged and have multiple peaks. The ruggedness of all three landscapes is also supported by the prevalence of epistasis between pairs of TFBS mutations (Supplementary Table S5). A particularly important form of epistasis is sign epistasis[24,93,94], because it can lead to multiple adaptive peaks [24,93,94] (see Supplementary Methods 7.5). Our landscapes contain up to 65% of mutation pairs with sign epistasis, a value that is especially high compared to the almost exclusively additive interactions of mutations in eukaryotic TFs[6,125].”

We now emphasize that prokaryotic TFBS landscapes, particularly for global regulators, appear to be substantially more rugged and epistatic than most previously characterized TFBS landscapes, and that this difference likely reflects fundamental biological distinctions between regulatory systems.

Revised emphasis and conclusions.

Following the reviewer’s suggestion, we have adjusted the emphasis of the manuscript accordingly. Rather than highlighting epistasis and contingency as generic evolutionary phenomena, we now present the extreme ruggedness of prokaryotic TFBS landscapes as a system-specific finding with important implications for the evolution of gene regulation. We explicitly note that this raises new questions for future work—such as why prokaryotic regulatory landscapes differ so markedly from eukaryotic ones, and how these differences shape evolutionary dynamics—which we now highlight in the Introduction and Discussion (Abstract; Introduction, lines 151-153, Discussion, lines 652–668). For example, we write in the discussion:

“… A possible reason for this greater incidence of epistasis lies in the nature of prokaryotic TFBSs. Specifically, prokaryotic TFBSs are at approximately 20bps twice as long as eukaryotic TFBSs[80,128] and exhibit symmetries that reflect the dimeric state of their cognate TFs[129–131]. These factors may increase the likelihood of intramolecular epistasis. Our observations raise important questions for future work, such as why the landscapes of prokaryotic TFBSs differ so dramatically from those of eukaryotic ones. And what do these differences imply for the evolutionary dynamics of gene regulation?”

We believe that these revisions substantially improve the clarity, motivation, and positioning of the manuscript, and directly address the reviewer’s concerns by making both the necessity and the novelty of the study clear from the outset.

(2) I am a bit concerned about the lack of uncertainties incorporated into the results. The authors acknowledge several key limitations of their approach, including the discreteness of the sort-seq bins in determining possible values of regulation strength, the existence of a large number of unsampled sequences in their genotype space, as well as measurement noise in the fluorescence readouts and sequencing. While the authors acknowledge the existence of these factors, I do not see much attempt to actually incorporate the effect of these uncertainties into their conclusions, which I suspect may be important. For example, given the bin size for the fluorescence in sort-seq, how confident are they that every sequence that appears to be a peak is actually a peak? Is it possible that many of the peak sequences have regulation strengths above all their neighbors but within the uncertainty of the fluorescence, making it possible that it's not really a peak? Perhaps such issues would average out and not change the statistical nature of their results, which are not about claiming that specific sequences are peaks, just how many peaks there are. Nevertheless, I think the lack of this robustness analysis makes the results less convincing than they otherwise would be.

We thank the reviewer for raising this important concern. We fully agree that uncertainties arising from experimental resolution, measurement noise in fluorescence and sequencing, and incomplete sampling of genotype space should be incorporated explicitly into the analysis. While these limitations were acknowledged qualitatively in the original manuscript, we recognize that a direct, quantitative assessment of their impact on our conclusions is essential to strengthen the robustness of the study.

We first clarify that regulation strength is not discretized in our analysis. For each TFBS, regulation strength is calculated as a continuous weighted average of fluorescence across all sorting bins, based on the sequencing read-count distribution of each sequence across bins. We clarified this information in the main text (Results, lines 201-203). Nevertheless, finite binning resolution and experimental noise introduce uncertainty in these estimates, which could in principle affect the identification of local peaks.

Importantly, our study does not aim to assert that specific TFBS sequences are definitively peaks. Rather, our focus is on landscape-level statistical and topological properties—such as ruggedness, the abundance and distribution of peaks, and the evolutionary accessibility of strong regulation. We therefore centered our new analyses on testing whether these conclusions are robust to experimentally plausible sources of uncertainty, rather than on the identity of individual peaks.

To address the reviewer’s concern, we performed two complementary analyses. The first evaluates whether the observed ruggedness of the landscapes could arise as an artifact of incomplete sampling. It addressed the effects of missing genotypes and the possibility of spurious peak identification due to unsampled neighbors. Sparse sampling can introduce opposing biases: true peaks may be missed, while other genotypes may be falsely classified as peaks because fitter neighbors are absent. As shown for uncorrelated random (House-of-Cards) landscapes (Kauffman & Levin, 1987), these effects can partially cancel.

In this analysis, we constructed a null model by randomly permuting regulation strengths across the mapped genotype network while preserving its topology. The number of peaks in these randomized landscapes is only modestly higher than in the empirical data, indicating that the measured landscapes are close to the maximal ruggedness compatible with the sampled network (Results, lines 308–320).

In addition, we quantified potential sampling bias by analyzing genotype connectivity. Here we defined the relative connectivity of a genotype as the fraction of possible single-mutant neighbors for which we had measured regulation strength. We observed only a very weak correlation between connectivity and regulation strength (R=-0.1, -0.1, 0.01 for the CRP, Fis, and IHF landscapes, Figures S13-S15). Similarly, the relative connectivity of peak genotypes is only weakly correlated with their regulation strength (R=-0.05, -0.04, 0.06 for the CRP, Fis, and IHF landscapes). (Results, lines 321–330), indicating that strongly regulating genotypes are not preferentially oversampled or undersampled (Results, lines 321–330).

The second, and most important, analysis directly addresses the reviewer’s concern that experimental uncertainty could affect peak classification and, consequently, landscape navigability. We explicitly incorporated experimentally measured, genotype-specific noise estimates from biological replicates when comparing fitness values between neighboring genotypes. Using these uncertainty-aware comparisons, we then recomputed adaptive-walk dynamics and genotype visitation frequencies on the resulting noisy landscapes.

We observe strong correlations between visitation frequencies in the noise-free and noisy landscapes across all three transcription factors (new Supplementary Figure S35), indicating that evolutionary accessibility patterns are robust to realistic levels of experimental uncertainty. These analyses are described in the revised Results (lines 622–636) and in a new Supplementary Methods section (“Incorporation of experimental uncertainty into adaptive walks”).

Reviewer #2 (Public review):

The authors aim to investigate the ability of evolution to create strong transcription factor binding sites (TFBSs) de novo in E. coli. They focus on three global transcriptional regulators: CRP, Fis, and IHF, using a massively parallel reporter assay to evaluate the regulatory effects of over 30,000 TFBS variants. By analyzing the resulting genotype-phenotype landscapes, they explore the ruggedness, accessibility, and evolutionary dynamics of regulatory landscapes, providing insights into the evolutionary feasibility of strong gene regulation. Their experiments show that de novo adaptive evolution of new gene regulation is feasible. It is also subject to a blend of chance, historical contingency, and evolutionary biases that favor some peaks and evolutionary paths.

(1) Strengths of the methods and results:

The authors successfully employed a well-designed sort-seq assay combined with high-throughput sequencing to map regulatory landscapes. The experimental design ensures reliable measurement of regulation strengths. Their system accounts for gene expression noise and normalizes measurements using appropriate controls.

Comprehensive Landscape Mapping:

The study examines ~30,000 TFBS variants per transcription factor, providing statistically robust and thorough maps of the regulatory landscapes for CRP, Fis, and IHF. The landscapes are rigorously analyzed for ruggedness (e.g., number of peaks) and epistasis, revealing parallels with theoretical uncorrelated random landscapes.

Evolutionary Dynamics Simulations:

Through simulations of adaptive walks under varying population dynamics, the authors demonstrate that high peaks in regulatory landscapes are accessible despite ruggedness. They identify key evolutionary phenomena, such as contingency (multiple paths to peaks) and biases toward specific evolutionary outcomes.

Biological Relevance and Novelty:

The author's work is novel in focusing on global regulators, which differ from previously studied local regulators (e.g., TetR). They provide compelling evidence that rugged landscapes are navigable, facilitating de novo evolution of regulatory interactions. The comparison of landscapes for CRP, Fis, and IHF underscores shared topographical features, suggesting general principles of global transcriptional regulation in bacteria.

(2) Weaknesses of the methods and results:

Undersampling of Genotype Space:

While the quality filtering of the data ensures robustness, ~40% of the TFBS space remains uncharacterized. The authors acknowledge this limitation but could improve the analysis by employing subsampling or predictive modeling.

We thank the reviewer for raising this point. We agree that undersampling of genotype space is an important limitation of our dataset and that, in principle, subsampling or predictive modeling approaches could be used to address missing genotypes. We have now clarified in the manuscript why these approaches are not straightforward in the context of our analyses and why we did not pursue them here.

Although approximately 40% of TFBS genotypes were removed during the filtering step due to lack of reliable measurements, this filtering step was necessary to ensure robust estimation of regulation strength from sort-seq data. Importantly, random subsampling of the genotypes in our data set would not alleviate this limitation, because many of our key analyses—such as peak identification, quantification of epistasis, and assessment of evolutionary accessibility—require combinatorially complete local neighborhoods in genotype space. Subsampling would remove mutational neighbors from many neighborhoods, and thus further limit our ability to characterize landscape topology.

Predictive modeling approaches could, in principle, be used to infer missing genotypes and reconstruct more complete landscapes. However, developing, experimentally validating, and benchmarking such models would not only substantially expand the scope of an already long paper, it would  also require additional assumptions about genotype–phenotype relationships that entail their own limitations. Our primary goal in this work was to provide the first large-scale empirical in vivo regulatory landscapes for global bacterial transcription factors, comprising tens of thousands of experimentally measured variants. We view these empirical landscapes as a necessary foundation upon which predictive modeling and landscape completion can be built in future, complementary studies.

We have now revised the Discussion (lines 760-770) to explicitly articulate these points and to clarify that, while undersampling remains a limitation, it does not invalidate the landscape-level conclusions we draw from the combinatorially complete neighborhoods present in our data. There we also outline predictive modeling as an important directions for future work.

For a more detailed answer regarding subsampling and peak classification, please also see our response to comment (2) of Reviewer #1.

Simplified Regulatory Architecture:

The study considers a minimal system of a single TFBS upstream of a reporter gene. While this may have been necessary for clarity, this simplification may not reflect the combinatorial complexity of transcriptional regulation in vivo.

Point well taken. We have added paragraph to state explicitly that the system we use to study gene regulation is much simpler than most in vivo regulatory circuits (Discussion, lines 797-802)

Lack of Experimental Validation of Simulations:

The adaptive walks are based on simulated dynamics rather than experimental evolution. Incorporating in vivo experimental evolution studies would strengthen the conclusions. Although this is a large request for the paper, that would not prevent publication.

We thank the reviewer for this important point. We fully agree that in vivo experimental evolution would provide a valuable and complementary way to validate the evolutionary dynamics inferred from our simulations. However, we ask for the reviewer's understanding that adding experimental evolution to an (already long) paper would go far beyond the scope of our study.

Also, the goal of our study was not to reproduce evolutionary trajectories experimentally, but to characterize the structure of large empirical regulatory landscapes, and to use these landscapes as a data-driven basis for exploring evolutionary accessibility under well-defined population-genetic assumptions. The adaptive walks we employ are parameterized directly from experimentally measured genotype–phenotype maps, and incorporate established fixation probabilities. Such walks have been widely used to study evolutionary dynamics on empirical landscapes when experimental evolution is not tractable, because it would involve tens of thousands of genotypes that represent small mutational targets and would thus take a long time to evolve.

An additional issue related to the feasibility of experimental evolution is that performing in vivo experimental evolution for the regulatory landscapes analyzed here would require tracking large populations across a combinatorially vast TFBS space, while simultaneously measuring regulatory phenotypes for thousands of evolving lineages, which is currently not experimentally feasible. This is another reason why simulation-based approaches have been the standard method for linking large-scale empirical landscapes to evolutionary dynamics in both theoretical and experimental studies.

Furthermore, our conclusions are intentionally framed at the level of statistical and landscape-wide properties (e.g., accessibility of high peaks, contingency, and evolutionary bias), rather than at the level of specific mutational trajectories. As such, they do not rely on the precise reproduction of any single evolutionary path, but on aggregate patterns that are robust to reasonable variation in population-genetic parameters.

In sum, we do not view experimental evolution as essential for the conclusions we draw, but as an important and exciting direction for future work that may be enabled by the landscapes we have experimentally mapped.

Impact on the Field:

This study advances our understanding of adaptive landscapes in gene regulation and offers a critical step toward deciphering how global regulators evolve de novo binding sites. The findings provide foundational insights for synthetic biology, evolutionary genetics, and systems biology by highlighting the evolutionary accessibility of strong regulation in bacteria.

Utility of Methods and Dat

The sort-seq approach, combined with landscape analysis, provides a robust framework that can be extended to other transcription factors and systems. If made publicly available, the study's data and code would be valuable for researchers modeling transcriptional regulation or studying evolutionary dynamics.

Additional Context:

The study builds on a growing body of work exploring regulatory evolution. For instance, recent studies on local regulators like TetR and AraC have revealed high ruggedness and epistasis in TFBS landscapes. This study distinguishes itself by focusing on global regulators, which are more biologically complex and influential in bacterial gene networks. The observed evolutionary contingency aligns with findings in other biological systems, such as protein evolution and RNA folding landscapes, underscoring the generality of these evolutionary principles.

Conclusion:

The authors successfully mapped the genotype-phenotype landscapes for three global regulators and simulated evolutionary dynamics to assess the feasibility of strong TFBS evolution. They convincingly demonstrate that ruggedness and epistasis, while prominent, do not preclude the evolution of strong regulation. Their results support the notion that gene regulation evolves through a blend of chance, contingency, and evolutionary biases.

This paper makes a significant contribution to the understanding of regulatory evolution in bacteria. While minor limitations exist, the authors' methods are robust, and their findings are well-supported. The work will likely be of broad interest to researchers in molecular evolution, synthetic biology, and gene regulation.

We thank the reviewer for their thorough evaluation and for their supportive opinion of this paper.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Line 28 (Abstract): "Landscape ruggedness does not prevent the evolution of strong regulation, because more than 10% of evolving populations can attain one of the highest peaks." I did not find this interpretation very convincing; only 10% of populations being able to achieve strong regulation sounds to me like ruggedness DOES impede adaptation in the vast majority of cases.

We thank the reviewer for this thoughtful comment and agree that our original phrasing in the Abstract overstated this conclusion. We did not intend to imply that landscape ruggedness has only a minor effect on adaptation. On the contrary, our results clearly show that ruggedness strongly constrains evolutionary outcomes and prevents the majority of evolving populations from reaching the globally highest regulatory peaks. We have therefore toned down the wording in both the Abstract and the Discussion (lines 670-679) to reflect this more accurately. For example, in the abstract we now state

“Nonetheless, evolutionary simulations show that ~10% of evolving populations can reach a peak of strong regulation, a proportion that is significantly greater than in comparable random landscapes.”

In the discussion we state:

“… Specifically, our evolutionary simulations show that 10% of populations with a size typical of E. coli reach one of the highest peaks. This percentage is significantly higher than in randomized landscapes (Supplementary Methods 9; Supplementary Figure S30)"

Our intended interpretation was more limited: namely, that ruggedness does not fully preclude the evolution of strong regulation. In highly rugged landscapes with extensive sign epistasis—whose topological properties approach those of uncorrelated random landscapes—the a priori expectation is that access to the strongest peaks could be vanishingly rare or effectively impossible under Darwinian evolution. In this context, observing that a non-negligible fraction of populations (on the order of 10%) can reach one of the highest peaks suggests that strong regulation remains evolutionarily attainable, even though it is far from guaranteed.

Motivated by the reviewer’s suggestion, we also added a null-model analysis that makes this point more explicitly and quantitatively. Specifically, we constructed randomized landscapes by permuting regulation-strength values across genotypes while preserving the experimentally sampled genotype network topology and all parameters of the evolutionary simulations (Supplementary Methods 9, “Randomized landscape null model for peak accessibility”). We then repeated the adaptive-walk simulations on these shuffled landscapes. This null model provides an expectation for peak accessibility in landscapes with identical sampling, neighborhood structure, and evolutionary dynamics, but without genotype–phenotype correlations.

Using this null model, we find that the fraction of populations that reach high peaks in the empirical landscapes is substantially higher than expected by chance alone (new Supplementary Figure S30; Results, lines 504–516). Specifically, across the three transcription factors, empirical landscapes exhibit on average a ~3-fold higher accessibility of high regulatory peaks than shuffled landscapes. This comparison does not weaken the conclusion that ruggedness strongly impedes adaptation; rather, it shows that the structure of the measured genotype–phenotype landscapes enables greater accessibility of strong regulation than would be expected in equally rugged but unstructured landscapes.

In response to the reviewer’s concern, we have revised the abstract and main text to avoid the phrase “does not prevent” and to more accurately convey this balance between constraint and accessibility. We now emphasize that ruggedness strongly constrains adaptation, while still allowing access to strong regulatory peaks at rates that exceed null expectations. (Discussion, lines 512-516). For example, in the discussion we state:

“… In sum, rugged regulatory landscapes strongly constrain evolutionary trajectories, yet do not render the evolution of strong regulation vanishingly rare. Instead, strong regulatory phenotypes remain evolutionarily attainable at levels that exceed null expectations, even though they are reached by only a minority of evolving populations.”

We believe that the revised wording, together with the added null-model analysis more faithfully represents our results and strengthens the quantitative interpretation of accessibility in these landscapes.

(2) Line 123: I found the explanation of the plasmid system and the accompanying SI figures (Figures S1 and S2) confusing in terms of how many plasmids there were. In particular, the Figure S1 graphics show the plasmid specifically with CRP but the text in the graphic and in the caption refers to the plasmid pCAW-Sort-Seq-V2 (which, according to Table S1, isn't that just the base plasmid without any TF?). Figure S2 also shows the plasmid with CRP and does specify pCAW-Sort-Seq-V2-CRP-CRP0 in the graphic, but then the caption refers again only to the base plasmid pCAW-Sort-Seq-V2. I recommend the authors clarify these items for readers who might want to reproduce or build upon their system. In particular, I recommend the main text explain more explicitly that they generate three versions of this plasmid (one for each TF), and then on the backgrounds of each of those three plasmids, a whole library with all the binding site variants.

We thank the reviewer for pointing out this lack of clarity. We agree that the original description of the plasmid system and the accompanying Supplementary Figures S1 and S2 could be confusing with respect to how many plasmids were used and how they differ.

To clarify the experimental design, we start from a common backbone plasmid, pCAW-Sort-Seq-V2, which contains all shared regulatory and reporter elements but does not encode any transcription factor. From this backbone, we generated three distinct TF-specific plasmids, each carrying one of the transcription factors studied here—CRP, Fis, or IHF—resulting in pCAW-Sort-Seq-V2-CRP, pCAW-Sort-Seq-V2-Fis, and pCAW-Sort-Seq-V2-IHF. On the background of each TF-specific plasmid, we then constructed a complete library of plasmids containing all variants of the corresponding TF binding site cloned upstream of the reporter gene.

We have revised the main text to explicitly describe this plasmid hierarchy and library construction strategy and to clarify that three TF-specific plasmids were generated prior to TFBS library construction (Results, Landscape mapping section; lines 159–193). In addition, we have redesigned Supplementary Figures S1 and S2 to facilitate understanding of the plasmid system. Specifically, these figures now clearly distinguish between the base plasmid backbone and the TF-specific plasmid derivatives. Also, the plasmid names shown in the graphics and captions are now consistent with those listed in Supplementary Table S1. Upon final publication, we will also deposit the sequences of all plasmids in Addgene to further facilitate reproducibility.

(3) Line 135: Can the authors clarify whether these TFs are essential in these media conditions and, if not, why? I was expecting them to be so given the core functions of these TFs as described in the Introduction, but then Figure S3 appears to show that all knockouts are viable.

We thank the reviewer for raising this important point and apologize for the lack of clarity in the original version of the manuscript. The transcription factors CRP, Fis, and IHF are not essential for viability under the growth conditions used in this study, but they are important for optimal growth and cellular fitness, consistent with their roles as global regulators.

Under our experimental conditions, single-gene knockout strains (Δcrp, Δfis, and Δihf) are viable but exhibit slower growth dynamics compared to the wild-type strain, reflecting impaired regulation of core cellular processes (Supplementary Figure S3). This behavior is consistent with previous work showing that many global transcriptional regulators in E. coli are conditionally essential or strongly fitness-affecting, rather than absolutely essential under standard laboratory conditions.

Importantly, while single knockouts remain viable, double mutants involving these global regulators are not viable, indicating substantial functional redundancy and network-level essentiality among global transcription factors. This explains why each TF can be studied individually in isolation, while combinations of deletions cannot be maintained.

We have now clarified this point in the Results section by explicitly stating that the knockout strains show reduced growth rates but reach comparable cell densities during late exponential or early stationary phase, the growth phase at which all measurements were performed (Results, Landscape mapping section; lines 185–193). This clarification reconciles the apparent discrepancy between the biological importance of these transcription factors discussed in the Introduction and the viability of the single-knockout strains shown in Supplementary Figure S3.

(4) Lines 141 and 227: The authors appear to refer to two different citations for different versions of RegulonDB (refs. 47 and 66). Did they actually use both versions for different purposes (if so, why?), or is this a typo?

We thank the reviewer for noticing this inconsistency. We did not use two different versions of RegulonDB. The two separate references were an error. We have now corrected this by using a single, consistent RegulonDB citation in both locations.

(5) Line 166 (Figure 1 caption): I think 2^8 here should be 4^8.

Thank you. We have corrected “2⁸” to “4⁸” in the Figure 1 caption.

(6) Figure 2Are the distributions in Figure 2a (regulation strengths across all TFBSs in the libraries) equivalent to the distributions in Figures S4-S6 (direct fluorescence readout from cell sorting), just transformed from fluorescence to regulation strength? If so I think that would be helpful to clarify, perhaps in the captions to Figures S4-S6 so that it's clear these contain the same information.

No. Figures S4–S6 and Figure 2a do not show the same distributions. Figures S4–S6 display the raw fluorescence distributions obtained from cell sorting, whereas Figure 2a shows regulation strengths (S), which are derived quantities computed from these fluorescence data. Specifically, regulation strength is calculated as a weighted average over fluorescence bins using the sequencing read distribution for each TFBS (see Methods, “Regulation strengths”).

To clarify this relationship, we have revised the main text (lines 201-203 and Figure 1b-c), to explicitly state how regulation strengths (S) were calculated.

(7) Figure 2b: Can the authors label each logo/frequency matrix with its corresponding TF name in the graphic itself? I think this is only implied in the caption.

We have updated Figure 2b to label each sequence logo / frequency matrix directly in the graphic with its corresponding transcription factor name (CRP, Fis, or IHF), in addition to mentioning these names in the caption. This change clarifies the figure and makes the TF identity immediately apparent to the reader.

(8) Lines 290 and 298 (Figure 2 caption): The labels for panels b and c appear to be swapped in the caption.

We thank the reviewer for pointing this out. The labels for panels b and c in the Figure 2 caption were indeed swapped. This has now been corrected.

(9) Line 379: There is a missing period at the end of this line.

We have added the missing period at the end of this line.

(10) Line 400 (Figure 3 caption): There is a missing subtitle for panel c in the caption for this figure (all other panels seem to have bolded subtitles in their captions).

We have added the missing subtitle for panel c in the Figure 3 caption to match the formatting of the other panels.

(11) Line 583: There is a missing period after "Methods 7.5)".

We have added the missing period after “Methods 7.5)”.

(12) Line 641: "All three landscapes highly rugged" should probably be "All three landscapes are highly rugged".

We have corrected the sentence to read “All three landscapes are highly rugged.”

I'm surprised that the scav-5 and scav-6 paralogs were both able to reduce the large LD phenotype to the same extent as scav-4 (there doesn't appear to be significant difference between the mutants). To me this suggests either they each contribute a third of the BCFA uptake, or that they operate together to internalize BCFAs. The scav-4;scav-6 double mutant suggests the first idea isn't correct as you don't see a stronger effect there. Do you think its possible these transporters are working as a complex? I would be interested to see if you can rescue each of these mutants with scav-4 expression, or if rescue requires all receptors to be present.

Author response:

The following is the authors’ response to the previous reviews

eLife Assessment

This study offers valuable insights into how humans detect and adapt to regime shifts, highlighting dissociable contributions of the frontoparietal network and ventromedial prefrontal cortex to sensitivity to signal diagnosticity and transition probabilities. The combination of an innovative instructed-probability task, Bayesian behavioural modeling, and model-based fMRI analyses provides a solid foundation for the main claims; however, major interpretational limitations remain, particularly a potential confound between posterior switch probability and time in the neuroimaging results. At the behavioural level, reliance on explicitly instructed conditional probabilities leaves open alternative explanations that complicate attribution to a single computational mechanism, such that clearer disambiguation between competing accounts and stronger control of temporal and representational confounds would further strengthen the evidence.

Thank you. In this revision, we addressed Reviewer 3’s remaining concern on the potential confound between posterior probability and time in neuroimaging results. First, as suggested by the reviewer, we provided images of activations for the effect of Pt and delta Pt after controlling for intertemporal prior in GLM-2. Second, we compared the effect of Pt and delta Pt between GLM-1 (without intertemporal prior) and GLM-2 (with intertemporal prior) and showed the results in a new figure (Figure 4).

Regarding issue on reliance on explicitly instructed probabilities, we wish to point out that most of the concerns such as response mode and regression to the mean were addressed in the original behavioral paper by Massey and Wu (2005). Please see our response to this point in detail in Weakness (2) posted by Reviewer 3.

Public Reviews:

Reviewer #1 (Public review):

Summary:

The study examines human biases in a regime-change task, in which participants have to report the probability of a regime change in the face of noisy data. The behavioral results indicate that humans display systematic biases, in particular, overreaction in stable but noisy environments and underreaction in volatile settings with more certain signals. fMRI results suggest that a frontoparietal brain network is selectively involved in representing subjective sensitivity to noise, while the vmPFC selectively represents sensitivity to the rate of change.

Strengths:

- The study relies on a task that measures regime-change detection primarily based on descriptive information about the noisiness and rate of change. This distinguishes the study from prior work using reversal-learning or change-point tasks in which participants are required to learn these parameters from experiences. The authors discuss these differences comprehensively.

- The study uses a simple Bayes-optimal model combined with model fitting, which seems to describe the data well. The model is comprehensively validated.

- The authors apply model-based fMRI analyses that provide a close link to behavioral results, offering an elegant way to examine individual biases.

Weaknesses:

The authors have adequately addressed my prior concerns.

Thank you for reviewing our paper and providing constructive comments that helped us improve our paper.

Reviewer #3 (Public review):

Thank you again for reviewing the manuscript. In this revision, we focused on addressing your concern on the potential confound between posterior probability and time in neuroimaging results. First, we presented whole-brain results of subjects’ probability estimates (Pt, their subjective posterior probability of switch) after controlling for the effect of time on probability of switch (the intertemporal prior). Second, we compared the effect of probability estimates (Pt) on vmPFC and ventral striatum activity—which we found to correlate with Pt—with and without including intertemporal prior in the GLM. These results will be summarized in a new figure (Figure 4) in the revised manuscript.

As suggested by the reviewer, we also added slice-by-slice images of the whole-brain results on Pt and delta Pt in the supplement in addition to the Tables of Activation so that the activated brain regions can be clearly seen through these images.

This study concerns how observers (human participants) detect changes in the statistics of their environment, termed regime shifts. To make this concrete, a series of 10 balls are drawn from an urn that contains mainly red or mainly blue balls. If there is a regime shift, the urn is changed over (from mainly red to mainly blue) at some point in the 10 trials. Participants report their belief that there has been a regime shift as a % probability. Their judgement should (mathematically) depend on the prior probability of a regime shift (which is set at one of three levels) and the strength of evidence (also one of three levels, operationalized as the proportion of red balls in the mostly-blue urn and vice versa). Participants are directly instructed of the prior probability of regime shift and proportion of red balls, which are presented on-screen as numerical probabilities. The task therefore differs from most previous work on this question in that probabilities are instructed rather than learned by observation, and beliefs are reported as numerical probabilities rather than being inferred from participants' choice behaviour (as in many bandit tasks, such as Behrens 2007 Nature Neurosci).

The key behavioural finding is that participants over-estimate the prior probability of regime change when it is low, and under estimate it when it is high; and participants over-estimate the strength of evidence when it is low and under-estimate it when it is high. In other words participants make much less distinction between the different generative environments than an optimal observer would. This is termed 'system neglect'. A neuroeconomic-style mathematical model is presented and fit to data.

Functional MRI results how that strength of evidence for a regime shift (roughly, the surprise associated with a blue ball from an apparently red urn) is associated with activity in the frontal-parietal orienting network. Meanwhile at time-points where the probability of a regime shift is high, there is activity in another network including vmPFC. Both networks show individual differences effects, such that people who were more sensitive to strength of evidence and prior probability show more activity in the frontal-parietal and vmPFC-linked networks respectively.

Strengths

(1) The study provides a different task for looking at change-detection and how this depends on estimates of environmental volatility and sensory evidence strength, in which participants are directly and precisely informed of the environmental volatility and sensory evidence strength rather than inferring them through observation as in most previous studies

(2) Participants directly provide belief estimates as probabilities rather than experimenters inferring them from choice behaviour as in most previous studies

(3) The results are consistent with well-established findings that surprising sensory events activate the frontal-parietal orienting network whilst updating of beliefs about the word ('regime shift') activates vmPFC.

Weaknesses

(1) The use of numerical probabilities (both to describe the environments to participants, and for participants to report their beliefs) may be problematic because people are notoriously bad at interpreting probabilities presented in this way, and show poor ability to reason with this information (see Kahneman's classic work on probabilistic reasoning, and how it can be improved by using natural frequencies). Therefore the fact that, in the present study, people do not fully use this information, or use it inaccurately, may reflect the mode of information delivery.

In the response to this comment the authors have pointed out their own previous work showing that system neglect can occur even when numerical probabilities are not used. This is reassuring but there remains a large body of classic work showing that observers do struggle with conditional probabilities of the type presented in the task.

Thank you. Yes, people do struggle with conditional probabilities in many studies. However, as our previous work suggested (Massey and Wu, 2005), system-neglect was likely not due to response mode (having to enter probability estimates or making binary predictions, and etc.).

(2) Although a very precise model of 'system neglect' is presented, many other models could fit the data.

For example, you would get similar effects due to attraction of parameter estimates towards a global mean - essentially application of a hyper-prior in which the parameters applied by each participant in each block are attracted towards the experiment-wise mean values of these parameters. For example, the prior probability of regime shift ground-truth values [0.01, 0.05, 0.10] are mapped to subjective values of [0.037, 0.052, 0.069]; this would occur if observers apply a hyper-prior that the probability of regime shift is about 0.05 (the average value over all blocks). This 'attraction to the mean' is a well-established phenomenon and cannot be ruled out with the current data (I suppose you could rule it out by comparing to another dataset in which the mean ground-truth value was different).

More generally, any model in which participants don't fully use the numerical information they were given would produce apparent 'system neglect'. Four qualitatively different example reasons are: 1. Some individual participants completely ignored the probability values given. 2. Participants did not ignore the probability values given, but combined them with a hyperprior as above. 3. Participants had a reporting bias where their reported beliefs that a regime-change had occurred tend to be shifted towards 50% (rather than reporting 'confident' values such 5% or 95%). 4. Participants underweighted probability outliers, resulting in underweighting of evidence in the 'high signal diagnosticity' environment (10.1016/j.neuron.2014.01.020 )

In summary I agree that any model that fits the data would have to capture the idea that participants don't differentiate between the different environments as much as they should, but I think there are a number of qualitatively different reasons why they might do this - of which the above are only examples - hence I find it problematic that the authors present the behaviour as evidence for one extremely specific model.

We thank the reviewer for this comment. We thank you for putting out that there are alternative models that can describe the over- and underreaction seen in the dataset. Massey and Wu (2005) dealt with this possibility in their original paper. Their concern was not so much about alternative ways of modeling their results, but in terms of alternative psychological processes. For example, asymmetric noise accounts have been posited in the judgment and decision making literature as possible accounts of phenomena like over-confidence. They addressed what might be crudely called “regression/attraction to the mean” in two ways. First, they looked at median responses as well as mean responses (because medians are less affected by the regressive effect) and found the same patterns of over- and underreactions. Second, they also generated sequences that matched particular posterior probabilities (so that over- and underreaction cannot be explained by regression to the mean) and still found under- and overreactions.

We also wish to point out in the judgment and decision making literature starting from Edwards (1968), there is a long history of using normative Bayesian model as the starting model and subsequently develop quasi-Bayesian models (like the system-neglect model) to describe systematic deviations from the normative Bayesian.

Finally, we want to clarify that our primary goal is not to engage in model fitting exercise that examines different possible models. To us, what is more important is that system neglect is a psychologically motivated hypothesis. It is built on the idea that the lack of sensitivity to the system parameters is due to the fact that people focus primarily on the signals and secondarily on the system parameters that generate the signals. Massey and Wu (2005) dealt with a host of other potential explanations through experimental manipulations and data analysis. In this paper, we built on Massey and Wu to examine the neurocomputational basis that gives rise to over- and underreactions.

(3) Despite efforts to control confounds in the fMRI study, including two control experiments, I think some confounds remain.

For example, a network of regions is presented as correlating with the cumulative probability that there has been a regime shift in this block of 10 samples (Pt). However, regardless of the exact samples shown, Pt always increases with sample number (as by the time of later samples, there have been more opportunities for a regime shift)? To control for this the authors include, in a supplementary analysis, an 'intertemporal prior.' I would have preferred to see the results of this better-controlled analysis presented in the main figure. From the tables in the SI it is very difficult to tell how the results change with the includion of the control regressors.

Thank you. In response, we added a new figure, now Figure 4, showing the results of Pt and delta Pt from GLM-2 where we added the intertemporal prior as a regressor to control for temporal confounds. We compared Pt and delta Pt results in vmPFC and ventral striatum between GLM-1 and GLM-2. We also showed the results on intertemporal prior on vmPFC and ventral striatum from GLM-2.

On the other hand, two additional fMRI experiments are done as control experiments and the effect of Pt in the main study is compared to Pt in these control experiments. Whilst I admire the effort in carrying out control studies, I can't understand how these particular experiment are useful controls. For example, in experiment 3 participants simply type in numbers presented on the screen - how can we even have an estimate of Pt from this task?

We thank the reviewer for this comment. On the one hand, the effect of Pt we see in brain activity can be simply due to motor confounds and the purpose of Experiment 3 was to control for them. Our question was, if subjects saw the similar visual layout and were just instructed to press buttons to indicate two-digit numbers, would we observe the vmPFC, ventral striatum, and the frontoparietal network like what we did in the main experiment (Experiment 1)?

On the other hand, the effect of Pt can simply reflect probability estimates of that the current regime is the blue regime, and therefore not particularly about change detection. In Experiment 2, we tested that idea, namely whether what we found about Pt was unique to change detection. In Experiment 2, subjects estimated the probability that the current regime is the blue regime (just as they did in Experiment 1) except that there were no regime shifts involved. In other words, it is possible that the regions we identified were generally associated with probability estimation and not particularly about probability estimates of change. We used Experiment 2 to examine whether this were true.

To make the purpose of the two control experiments clearer, we updated the paragraph describing the control experiments on page 9:

“To establish the neural representations for regime-shift estimation, we performed three fMRI experiments (n = 30 subjects for each experiment, 90 subjects in total). Experiment 1 was the main experiment, while Experiments 2 to 3 were control experiments that ruled out two important confounds (Fig. 1E). The control experiments were designed to clarify whether any effect of subjects’ probability estimates of a regime shift, P_t, in brain activity can be uniquely attributed to change detection. Here we considered two major confounds that can contribute to the effect of P_t. First, since subjects in Experiment 1 made judgments about the probability that the current regime is the blue regime (which corresponded to probability of regime change), the effect of P_t did not particularly have to do with change detection. To address this issue, in Experiment 2 subjects made exactly the same judgments as in Experiment 1 except that the environments were stationary (no transition from one regime to another was possible), as in Edwards (1968) classic “bookbag-and-poker chip” studies. Subjects in both experiments had to estimate the probability that the current regime is the blue regime, but this estimation corresponded to the estimates of regime change only in Experiment 1. Therefore, activity that correlated with probability estimates in Experiment 1 but not in Experiment 2 can be uniquely attributed to representing regime-shift judgments. Second, the effect of P_t can be due to motor preparation and/or execution, as subjects in Experiment 1 entered two-digit numbers with button presses to indicate their probability estimates. To address this issue, in Experiment 3 subjects performed a task where they were presented with two-digit numbers and were instructed to enter the numbers with button presses. By comparing the fMRI results of these experiments, we were therefore able to establish the neural representations that can be uniquely attributed to the probability estimates of regime-shift.”

To further make sure that the probability-estimate signals in Experiment 1 were not due to motor confounds, we implemented an action-handedness regressor in the GLM, as we described below on page 19:

“Finally, we note that in GLM-1, we implemented an “action-handedness” regressor to directly address the motor-confound issue, that higher probability estimates preferentially involved right-handed responses for entering higher digits. The action-handedness regressor was parametric, coding -1 if both finger presses involved the left hand (e.g., a subject pressed “23” as her probability estimate when seeing a signal), 0 if using one left finger and one right finger (e.g., “75”), and 1 if both finger presses involved the right hand (e.g., “90”). Taken together, these results ruled out motor confounds and suggested that vmPFC and ventral striatum represent subjects’ probability estimates of change (regime shifts) and belief revision.”

(4) The Discussion is very long, and whilst a lot of related literature is cited, I found it hard to pin down within the discussion, what the key contributions of this study are. In my opinion it would be better to have a short but incisive discussion highlighting the advances in understanding that arise from the current study, rather than reviewing the field so broadly.

Thank you. We thank the reviewer for pushing us to highlight the key contributions. In response, we added a paragraph at the beginning of Discussion to better highlight our contributions:

“In this study, we investigated how humans detect changes in the environments and the neural mechanisms that contribute to how we might under- and overreact in our judgments. Combining a novel behavioral paradigm with computational modeling and fMRI, we discovered that sensitivity to environmental parameters that directly impact change detection is a key mechanism for under- and overreactions. This mechanism is implemented by distinct brain networks in the frontal and parietal cortices and in accordance with the computational roles they played in change detection. By introducing the framework in system neglect and providing evidence for its neural implementations, this study offered both theoretical and empirical insights into how systematic judgment biases arise in dynamic environments.”

Recommendations for the authors:

Reviewer #3 (Recommendations for the authors):

Thank you for pointing out the inclusion of the intertemporal prior in glm2, this seems like an important control that would address my criticism. Why not present this better-controlled analysis in the main figure, rather than the results for glm1 which has no effective control of the increasing posterior probability of a reversal with time?

Thank you for this suggestion. We added a new figure (Figure 4) that showed results of Pt and delta Pt from GLM-2. We also compared the effect of Pt and delta Pt between GLM-1 and GLM-2. We found that the effect of Pt and delta Pt did not differ between GLM-1 and GLM-2. GLM-1 and GLM-2 differed on whether various task-related regressors contributing to Pt, including the intertemporal prior, were included in the model. In GLM-1, those task-related regressors were not included. In GLM-2, the task-related regressors were included in addition to Pt and delta P.

The reason we kept results from GLM-1 (Figure 3) was primarily because we wanted to compare the effect of Pt between experiments under identical GLM. In other words, the regressors in GLM-1 was identical across all 3 experiments. In Experiments 1 and 2, Pt and delta Pt were respectively probability estimates and belief updates that current regime was the Blue regime. In Experiment 3, Pt and delta Pt were simply the number subjects were instructed to press (Pt) and change in number between successive periods (delta Pt).

Here is the section in the main text where we discussed the new Figure 4 on page 19-22:

We further examined the robustness of P_t and ∆P_t representations in vmPFC and ventral striatum in three follow-up analyses. In the first analysis, we implemented a GLM (GLM-2 in Methods) that, in addition to P_t and ∆P_t, included various task-related variables contributing to P_t as regressors. Specifically, to account for the fact that the probability of regime change increased over time, we included the intertemporal prior as a regressor in GLM-2. The intertemporal prior is the natural logarithm of the odds in favor of regime shift in the t-th period, , where q is transition probability and t = 1, …, 10is the period (Eq. 1 in Methods). It describes normatively how the prior probability of change increased over time regardless of the signals (blue and red balls) the subjects saw during a trial. Including it along with P_t would clarify whether any effect of P_t can otherwise be attributed to the intertemporal prior. We found that the results of P_t and ∆P_t in the vmPFC and ventral striatum in GLM-2 were identical to those in GLM-1 (Fig. 4): Fig. 4A was meant to depict the results in slices identical to those shown in Fig. 3B for results based on GLM-1. For slice-by-slice results, see Fig. S7 in SI for results based on GLM-1 and Fig. S9 for GLM-2. For Tables of activations, see Tables S1-S3 in SI for GLM-1 and Tables S7-S9 for GLM-2. In a separate, independent region-of-interest (ROI) analysis on vmPFC and ventral striatum (Fig. 4BC; see Independent regions-of-interest (ROIs) analysis in Methods for details), we further compared the effect of both P_t and ∆P_t between GLM-1 and GLM-2. For P_t, the difference between GLM-1 and GLM-2 was not significant (paired t-test, t(58) = −0.72, p = 0.47 in vmPFC, t(58) = −0.21, p = 0.83 in ventral striatum), while the effect of P_t from GLM-1 (one sample t-test, t(29) = −3,82, p <.01 in vmPFC; t(29) = −3.06, p <.01 in ventral striatum) and GLM-2 was significant (one-sample t-test, t(29) = −2.69, p =.01 in vmPFC; t(29) = −2.50, p .02 in ventral striatum). For ∆P_t, the difference between GLM-1 and GLM-2 was not significant (paired t-test, t(58) = −0.07, p =0.94 in vmPFC; t(58) = −0.14, p =0.88 in ventral striatum), while the effect of  from GLM-1 (one-sample t-test, t(29) = −3.12, p <.01 in vmPFC; t(29) = −4.14, p <.01 in ventral striatum) and GLM-2 was significant (one-sample t-test, t(29) = −2.92, p <.01 in vmPFC; t(29) = −3.59, p <.01 in ventral striatum). For the intertemporal prior, activity in both vmPFC and ventral striatum did not correlate significantly with the intertemporal prior (one-sample t-test, t(29) = −0.07, p =0.95 in vmPFC; t(29) = −0.53, p =0.60 in ventral striatum). All the t-tests described above were two-tailed. Taken together, these results suggest that vmPFC and ventral striatum represented P_t and ∆P_t regardless of whether the intertemporal prior and other task-related regressors contributing to P_t were included in the GLM. We also did not find that vmPFC and ventral striatum to represent the intertemporal prior. In the second analysis, we implemented a GLM that replaced P_t with the log odds of P_t, 1n (P_t/(1 - P_t)) (Fig. S10 in SI). In the third analysis, we implemented a GLM that examined P_t separately on periods when change-consistent (blue balls) and change-inconsistent (red balls) signals appeared (Fig. S11 in SI). Each of these analyses showed significant correlation with P_t in vmPFC and ventral striatum, further establishing the robustness of the P_t findings.

As a further point I could not navigate the tables of fMRI activations in SI and recommend replacing or supplementing these with images. For example I cannot actually find a vmPFC or ventral striatum cluster listed for the effect of Pt in GLM1 (version in table S1), which I thought were the main results? Beyond that, comparing how much weaker (or not) those results are when additional confound regressors are included in GLM2 seems impossible.

As suggested by the reviewer, we added slice-by-slice images showing the effect of Pt and delta Pt (Figure S9 in SI for GLM-2 and Figure S7 for GLM-1). The clusters in blue represent Pt effect, the clusters in orange represent delta Pt effect. As can be seen, both Pt and delta Pt are represented in the vmPFC and ventral striatum.

TikTok only shows the number of likes as an integer data type, meaning it tells me how many people liked a video, but it does not show different emotions like Facebook, where users can react with various feelings. So we cannot really tell whether people truly enjoyed the video or just saved or liked it to share with others. It does not clearly reflect viewers’ real feelings, including mine. Another example is text data such as usernames and profile pictures which are based on users’ personal preferences and do not necessarily reflect who they are in real life. This is why there are many fake accounts on social media, created for different purposes. Sometimes when scrolling on TikTok, I wonder why I see unfamiliar videos that I have never searched for or talked about. I think this happens because the platform collects data from my followers, and if they like certain types of videos, similar content may also appear on my feed.

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Reply to the reviewers

1. Point-by-point description of the revisions

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Reviewer #1 (Evidence, reproducibility and clarity (Required)):

In this study, the authors investigated the effect of nutritional stress (HSD and HFD) on cardiac function by assessing multiple parameters on adult flies. They next identified the adaptive transcriptomic changes in the heart in response to these nutritional stresses and screened for their roles under ND, HSD and HFD. They identified fit gene, encoding a satiety gene, expressed by cardiomyocytes and pericardial cells.

I think the characterisation is thorough; however, the conclusion is not well supported by the evidence. My main concern is that in many graphs, the difference between control and experiment is subtle, and, secondly, the authors showed some conflicting results (e.g. one RNAi showed a reduction of one parameter, however, the other independent RNAi did not. In this case, I believe the authors shouldn't conclude that the RNAi is functionally required, since the RNAis are meant to confirm each other.

First, we thank the reviewer for her/his constructive comments and suggestions. We obtained new results presented in the last version of the manuscript, which consistently support our conclusions and improve the study.

High-Sugar and High-Fat Diets modified cardiac performance

They assessed how HSD and HFD affect Adult fly heart performance. Instead of performing 3 weeks of dietary manipulation as has been done before by other groups, they put adult flies on HSD for 7 days and HFD for only 3 days.

We would like to clarify the nutritional challenge used. Cardiac function of flies was assessed at 10 days after emergence. Flies were put either in ND or HSD during these 10 days (ND and HSD conditions), or in ND for 7 days then transferred on HFD for 3days (HFD condition). Finally, all the females spent 10 days in a diet before being imaged or before hearts/brains dissection.

They found: HSD increases HP and SI, and reduces AI. The difference is too small and not consistent between different control lines. Also, when the difference is this small, p value does not tell much!

They probably intentionally induced a milder effect so that they could assess adaptive transcriptomic changes to this nutritional stress. In Fig. 1D SI is increased under HSD with control-KK, In Fig. S1C, SI is not changed under HSD with control-GD and control-GFP. Instead, DI is increased, which is also opposite to what they showed in Fig. 1 C. HFD increased ESD, EDD, SV, FS and CO.(Hypertrophy). This is not true with control-GD and control-GFP lines though! Comments: They have assessed many parameters in live animals with many different control lines, which is thorough. However, it is hard to draw any conclusions based on these conflicting results. Are these effect KK line specific?

Globally, we agree with the reviewer that the results, presented in the first version of the manuscript, for the control lines were difficult to understand due to the inconsistency of the phenotypes. In this revised version, we performed new results in Figure 1 and __S1 __regarding the effect of 10 days HSD and 3 days HFD exposure vs ND.

105 to 187 flies were imaged for the 3 control conditions, in the 3 diets concomitantly, to increase the power of our analysis. As mentioned in the main text (page 3, line 30-35; page 4, line 1-5), both diets deteriorate cardiac function with HFD leading to consistent phenotypes on heart diameters and rhythm and HSD milder effects. Indeed, the 3 control lines were uniformly affected by HFD after 3 days exposure, whereas 10 days in HSD was not sufficient to quantify a significant effect despite consistent the trends on several phenotypes (EDD, ESD, DI, AI and CO. These results revealed a different sensitivity of the cardiac performance when exposed to sugar and fat.

As described in the text, we were nevertheless confident that our approach would be good to investigate the early molecular dysregulations induced by sugar. This was the purpose of our analysis, presented in the follow-up of the manuscript.

Regarding the small differences measured in the phenotypes in HSD and HFD compared to ND, we would like to outline that the values presented are normalized values to control. Normalization is done for every independent experiment, performed at different dates, and permits the graphical representation of pooled values. Statistical analysis is performed using non-parametric Kruskal-Wallis test accordingly. Values are presented with the X axis cutting the Y axis at 0, this graphical representation also contributes to flattening the differences and p-values indicate their significance.

Analysis of the fly cardiac transcriptome upon nutritional stress

RNA seq to detect differentially expressed genes under HSD and HFD vs ND. Most DE genes are downregulated, which prompts them to assess how the downregulation of these genes adapts the animals to this nutritional stress.

High Sugar Diet downregulated 1c-metabolism and Leloir galactose pathways.

In this revised manuscript, we first present RT-qPCR validating the downregulation of Gnmt, Sardh and Galk expressions in the heart of 10days old HSD-fed females compared to ND-fed ones (Figure S3A).

We apologize for the confused explanations in the first version of the manuscript. We show new results in Figure 3 and __S3 __on the cardiac function of both Gnmt and Sardh, where following reviewer’s suggestion, both genes were knocked down in the heart in ND and Gnmt overexpressed in HSD. No available tools allowed us to test Sardh overexpression in HSD and we could not get some for Galk.

GNMT is downregulated under HSD and HFD.

In ND, GNMT knockdown increased ESD, EDD and CO. Sardh knockdown did the same? However, Sardh knockdown did not affect ESD significantly.

We reanalyze our first data and added new ones, comparing only knockdown or overexpression to the corresponding controls performed in concomitant experiments. Results are now shown in Figure 3C-E; S3C-H. Knocking down Gnmt in the heart increased HP, EDD, ESD and CO, Sardh knockdown in ND resulted in milder phenotypes but inducing significant hypertrophy in ND as Gnmt does. In both cases, FS was not impacted.

Both genes have been previously shown as beneficial to muscular function in time-restricted feeding context (Livelo et al., 2023, Nat.Comm.), illustrating that, even if both enzymes are involved in opposite reaction, their function has the same effect on organ/tissue function, as they did for heart diameters. The text corresponding to results and discussion were updated accordingly (pages 5, 11).

The conclusion here is: GNMT knockdown induces hypertrophy, similar to the effect of HFD.

In HSD, further knockdown of GNMT reduced (rescued) HP, suggesting downregulation of GNMT under HSD is adaptive. Should overexpress GNMT under HSD to see if this manipulation further increases HP, to claim GNMT downregulation is an adaptive change to high sugar stress.

We thank the reviewer for her/his suggestion. We now used UAS-GnmtWT (from FlyORF) to assess the role of Gnmt on cardiac function in HSD.

As shown in (Figure 3C-E; S3C,F), overexpressing Gnmt in the heart in HSD was sufficient to rescue some sugar induced phenotypes or to induce other dysfunctions, when compared to corresponding controls evaluated in the same experiments in ND and HSD. Notably, HP increase and CO decrease are rescued by Gnmt cardiac overexpression in HSD. Interestingly, the cardiac diastolic constriction induced by HSD is associated to increased FS and CO in this genotype in sugar diet. These new results strengthen the positive effect of Gnmt on cardiac function, improving it in HSD and preventing its deterioration in this diet.

Of note, Gnmt overexpression in ND did not trigger cardiac dysfunctions (data not shown).

The results and conclusions have been corrected.

Interestingly, HSD itself tends to decrease AI, a further knockdown of GNMT further decreases AI. This indicates GNMT downregulation under HSD contributes to AI reduction. Together, GNMT downregulation under HSD prevents HP from going higher, while its downregulation causes AI going down.

In the manscript, the authors claim that " Gnmt KD led reduced HP and AI, suggesting that it is able to counteract the effect of HSD observed in control flies on these phenotypes". This is not true according to the logic in Results section 1. As in section 1, the effect of HSD on AI is not significant, so the authors shouldn't say" HS tended to reduce AI".

Our reanalyzes and new results showed no Gnmt impact on AI, so these Figure panels were removed.

Why GNMT knockdown reduced FS under ND (Fig. S3C), while increasing FS under HSD (Fig. 3F)? If GNMT knockdown induces hypertrophy, I would expect it to increase FS.

Gnmt overexpression did not affect cardiac diameters in HSD, but it nevertheless led to an increased contractile efficacy compared to HSD controls (Figure S3F).

These new results strengthen the positive effect of Gnmt on cardiac function, preventing its deterioration in sugar diet. The text was modified accordingly.

High Fat Diet modulated CD36-scavenger receptor and Glut8 orthologues

In this revised manuscript, we present RT-qPCR validating the downregulation of Snmp1 expression and the slight upregulation of nebu’s in the heart of 10days old HFD-fed females compared to ND-fed ones (Figure S3B).

HFD: Snmp1 gene is downregulated, however, both overexpression and knockdown of Snmp1 in ND induced some phenotypes.

Indeed, as mentioned in the revised manuscript (page 6, lines 21-24), in heart of females fed ND, both Snmp1 knockdown (Snmp1KK) and overexpression (Snmp1WT) showed a reduction of EDD and ESD (Figure 3J; S3J) but FS is increased accordingly only in Snmp1KK.

As notified in the text, both downregulation and overexpression of Snmp1 led to side-phenotypes (page 6, lines 24-28): Snmp1KK exhibited abdominal fat increase (Figure S3K) and ostial cells seemed clearly malformed in Snmp1WT (Figure 3M). This may explain why the heart shows the same type of functional impairment in both genotypes.

We now discussed the hypothesis that these similar cardiac dysfunctions may result from Snmp1 being a regulator of organismal or cardiac lipid homeostasis. Indeed, increasing body fat content is deleterious as is increasing the import of fat in the cardiomyocytes. Finally, both affects cardiac cells’ health and functioning.

HFD: nebu has a role in regulating cardiac function under ND.

HSD and HFD revealed the secretory function of the heart

They identified diet-regulated secreted proteins that are required for cardiac dysfunction.

Cardiac Fit expression impacted Cardiac performance.

The author used Hand-G4 to knock down Fit using KK and GD lines, KK line showed a reduction in HP (Fig. 5A), but not GD line (Fig. S5D). How did the author conclude that Fit is required for cardiac function? Also, with the positive data, the difference is too subtle.

We apologize and agree that the contradictory or inconsistent results obtained with the two RNAi lines were confusing.

For this revised version, we first assess the effect of the two RNAi lines (KK and GD) on fit expression in the dissected hearts. RT-qPCR for KK line is presented in Figure S5A. GD line did not show a significant reduction of fit expression when expressed in the heart with Hand>, which can explain the former results presented (not shown but data are available). So, we removed all results obtained with the GD line in this revised version.

To confirm the KK effects, we used fit KO allele (fit81) and truncated version of fit, without its signal peptide (fitDeltaSP), which has a dominant negative effect, both previously published and validated (Sun et al. 2017, Nat. Comm.). These two mutants were used to investigate the cardiac function of fit in our analysis. Results presented in Figure 5 and S5 confirm the phenotypes already observed with the KK line when expressed with Hand> in the heart and with Lsp2> in the fat body.

Our results validate the effect of fit decrease on rhythmicity and contractility, the reverse effects being consistently observed in fit overexpression. In conclusion, we are confident in the requirement of Fit in the regulation of cardiac performance.

These new data are now included in the results section “Cardiac Fit expression impacted Cardiac performance” (pages 8-9)

**Referee cross-commenting**

i agree with the experiments proposed by reviewer 2.

Reviewer #1 (Significance (Required)):

The study aims to examine the effect of diet on cardiac function.

The strength is that a lot of characterisations were done.

the weakness is the functional data regarding fit could not be validated in two different RNAis, thus the evidence is not strong to support the conclusions.

We again would like to thank the reviewer for her/his remarks and suggestions. She/He highlights the weakness of the first analysis and this was an important and constructive feedbacks for us. We strengthened our results by increasing samples, reanalyzing data and performing mandatory new experiments that are now included in this revised version.

Reviewer #2 (Evidence, reproducibility and clarity (Required)):

In this manuscript, Khamvongsa-Charbonnier et al. reported a RNA-seq analysis and RNA interference screening on high-fat and high-sugar-induced cardiomyopathy in Drosophila. The authors uncovered novel genes in 1C-metabolism, galactose metabolism, CD36-scavenger receptor and glucose transporter, as adaptative factors of cardiac function under high-fat and high-sugar treatment. The authors also identified a satiety hormone, Fit, as a cardiokine to control food intake and , expressed by dilp5 secretion. In summary, this study leverages the powerful genetic model Drosophila to uncover a number of new factors in regulating cardiac function under nutritional stresses and potentially offers new insights into molecular mechanisms underlying diet-related cardiac diseases. I have a few concerns, as listed below.

First, we would like to thank the reviewer for her/his comments and suggestions that deeply help us to improve the take-home messages of our manuscript. Following her/his recommendations and suggestions, we can now present a revised and stronger version of our manuscript.

1. Quantitative RT-PCR is required to validate the expression patterns of candidate genes identified from the RNAseq analysis.

RT-qPCR have been performed on hearts dissected from 10 days old females fed ND, HSD or HFD. Gnmt, Sardh and Galk validated downregulation are presented in Figure S3A, Snmp1 downregulation and nebu upregulation (trend but non-significant) in Figure S3B, fit downregulation in Figure S5A.

The authors state that the dysregulated gene expression patterns reflect acute adaptation to HSD and HFD stresses. Most of the candidate genes in this study were downregulated upon HSD and HFD. However, it is recommended that overexpression of these genes, rather than knockdown, is needed to confirm whether the downregulation of these candidate genes upon stresses is an adaptative response.

We agree with the reviewer and followed her/his recommendation when tools were accessible for our analysis.

For example, HSD feeding induces the heart period. Knocking down Gnmt, specifically in the heart, under the HSD feeding changes can reduce the heart period. This evidence is insufficient to suggest the protective role of Gnmt under the HSD diet. Gnmt has already been downregulated under the HSD. Further knockdown of Gnmt, instead of returning the Gnmt expression to normal levels, to protect cardiac contractile performance complicates the model.

We thank the reviewer for her/his suggestion. We used UAS-*GnmtWT * (from FlyORF) to perform these experiments.

As shown in (Figure 3C-E; S3C,F), knocking down Gnmt in the heart increased HP, EDD, ESD and CO. In the same Figure panels and in Figure S3F, we showed that overexpressing Gnmt with Hand> in HSD was sufficient to rescue some sugar induced phenotypes or to induce some, when compared to corresponding controls evaluated in the same experiments in ND and HSD. Gnmt overexpression in ND did not trigger cardiac dysfunctions (data not shown).

HP increase and CO decrease are rescued by Gnmt cardiac overexpression in HSD. Interestingly, the cardiac constriction induced by HSD is not rescued by Gnmt overexpression, but it is enough to increase FS and CO in sugar diet. These new results strengthen the positive effect of Gnmt on cardiac function, improving it in HSD and preventing its deterioration in this diet.

Sardh knockdown in ND, resulted in milder phenotypes but induced significant hypertrophy in ND as Gnmt does. No available tools allowed us to test its overexpression in HSD.

Nevertheless, as mentioned and discussed in the manuscript (page 5, line 27-30; page 11, lines 11-14), such protective role of muscular function and integrity has already been characterized in fly IFM in time-restricted feeding experiments for Gnmt and Sardh (Livelo et al., 2023, Nat.Comm.). Our experiments show that both genes encounter the same role in cardiac function upon nutritional stresses. The text was modified accordingly.

The authors suggest that the effect of nebu on heart contractility is not dependent on diet. However, based on the result from Figure 3O-P, the HFD treatment blocks the effect of nebu knockdown on heart contractility. The authors need to further explain these results and modify their conclusions accordingly.

We completely agree with the reviewer. We did not correctly analyze these results. We reanalyze our data, taking into account only the experiments of nebu knockdown that were performed in ND and in HFD concomitantly. Results are shown in Figure 3O-P; S3L-N.

As mentioned in the manuscript (page 7, lines 3-8), nebu knockdown led to identical HP decrease in both diets but its constrictive effect (reduction of heart diameters) in ND is abrogated by fat diet.

We modified the text accordingly in the results and discussion (page 7, lines 8-11; page 12, lines 7-12).

It is a bit confusing that knockdown of fit using Hand-Gal4 induced food intake, but knockdown of fit using tin-Gal4 or Dot-Gal4 did not significantly induce food intake (Fig 6A). The author did not provide any explanation of these results. What is even more confusing is that overexpressing fit using Dot-Gal4 decreased food intake, but overexpressing fit using Hand-Gal4 or tin-Gal4 did not significantly decrease food intake (Fig 6B). Why was the strong food intake phenotype not observed using Hand-Gal4 in both experiments? These confusing results lead to a question, which cell type is responsible for the production of cardiokine, Fit?

We apologize for the misleading results presented in the initial manuscript. We hope that our revised version will clarify Fit function regarding its remote impact.

Concerning the requirement of Fit function and the cell types that produces Fit, the results we obtained when evaluating cardiac performance strongly suggest that both cardiomyocytes and pericardial cells are important and recapitulate the effect of Hand> (Figure 5A-C; S5G-H).

In the case of food intake measurements, we now present results with newly performed food intake experiments for the Hand>fitWT (Figure 6D). They show a significant reduction of food intake in this condition, corroborating the results obtained with Dot>. We add a clarification in the manuscript for this point (page 10, lines 11-16).

When testing the role of cardiac Fit in Dilp5 secretion, the authors subjected flies to starvation stress. However, the main focus of the present study is on HSD and HFD. The RNAseq analysis showed that Fit expression was downregulated by both HSD and HFD. Can the authors show that Dilp5 secretion is reduced by both HSD and HFD? Most importantly, can the authors test whether overexpression of cardiac Fit blocks HSD- or HFD-reduced Dilp5 secretion?

We understand the point raised by the reviewer. First of all, we wanted to correlate the measured impact on food intake, when manipulating fit expression in the heart, to the level of Dilp release, as it has been used and validated in (Sun et al. 2017, Nat. Comm.). In this purpose, we used the same approach and protocol and results are shown in Figure 6 E-F.

As mentioned by the reviewer, fit expression is downregulated in both HSD and HFD (which we confirmed by RT-qPCR in Figure S5A). As suggested by the reviewer, we performed Dilp5 immunostaining on CNS from females that were fed HSD of HFD for 10 days. Our results, in Figure 6B (left panels) and corresponding quantifications in Figure 6C, show that both diets strongly induce a decrease in Dilp5 amount in the IPCs and that it was not due to an altered Dilp2 or Dilp5 expression in the CNS (Figure S6A). In this condition, overexpressing fit, which has a promoting effect on Dilp secretion (Figure 6B, right panels ND), may only have an additive effect. This is shown in Figure 6B-C.

Reviewer #2 (Significance (Required)):

In summary, this study leverages the powerful genetic model Drosophila to uncover a number of new factors in regulating cardiac function under nutritional stresses and potentially offers new insights into molecular mechanisms underlying diet-related cardiac diseases.

We again would like to thank the reviewer for her/his remarks and suggestions. Her/His important and constructive feedbacks helped us to improve and strengthen our study. Despite the weak points of the first version, she/he had supportive feedback and we deeply thank her/him. This revised version had improved results and analysis, thanks to the use of new genetic tools that strengthen this analysis.

Author Response:

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

Public Reviews:

Reviewer #1 (Public review):

Weaknesses:

Despite this compelling data regarding the protective role of HSF1 in the febrile response, what remains unexplained and complicates the authors' model is the observation that losing LvHSF1 at 'normal' temperatures of 25 ℃ is not detrimental to survival, even though viral loads increase and nSWD is likely still subject to LvHSF1 regulation. These observations suggest that WSSV infection may have other detrimental effects on the cell not reflected by viral load and that LvHSF1 may play additional roles in protecting the organism from these effects of WSSV infection, such as perhaps, perturbations to protein homeostasis. This is worth discussing, especially in light of the rather complicated roles of hormesis in protection from infection, the role of HSF1 in hormesis responses, and the findings from other groups that the authors discuss.

We are grateful for your unbiased advice by reviewer. And we have added the description about the role of HSF1 in hormesis responses in discussion in Lines 422-425 in the revised manuscript. Thank you.

Reviewer #2 (Public review):

Temperature is a critical factor affecting the progression of viral diseases in vertebrates and invertebrates. In the current study, the authors investigate mechanisms by which high temperatures promote anti-viral resistance in shrimp. They show that high temperatures induce HSF1 expression, which in turn upregulates AMPs. The AMPs target viral envelope proteins and inhibit viral infection/replication. The authors confirm this process in drosophila and suggest that there may be a conserved mechanism of high-temperature mediated anti-viral response in arthropods. These findings will enhance our understanding of how high temperature improves resistance to viral infection in animals.

The conclusions of this paper are mostly well supported by data, but some aspects of data analysis need to be clarified and extended. Further investigation on how WSSV infection is affected by AMP would have strengthened the study.

We are grateful for your unbiased advice by reviewer. We have provided additional experimental evidence and supplementary instructions in the revised manuscript. Thank you.

Reviewer #3 (Public review):

In the manuscript titled "Heat Shock Factor Regulation of Antimicrobial Peptides Expression Suggests a Conserved Defense Mechanism Induced by Febrile Temperature in Arthropods", the authors investigate the role of heat shock factor 1 (HSF1) in regulating antimicrobial peptides (AMPs) in response to viral infections, particularly focusing on febrile temperatures. Using shrimp (Litopenaeus vannamei) and Drosophila S2 cells as models, this study shows that HSF1 induces the expression of AMPs, which in turn inhibit viral replication, offering insights into how febrile temperatures enhance immune responses. The study demonstrates that HSF1 binds to heat shock elements (HSE) in AMPs, suggesting a conserved antiviral defense mechanism in arthropods. The findings are informative for understanding innate immunity against viral infections, particularly in aquaculture. However, the logical flow of the paper can be improved.

We are grateful for the positive comments and the unbiased advice by reviewer. We have improved the logical flow of the paper and added corresponding instructions in the revised manuscript. Thank you.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Figure 1: The analysis compares Group TW to Group W (not the other way around).

Thank you very much. To uncover the molecular mechanisms by which high temperature restricts WSSV infection, two shrimp groups, Group TW and Group W, were cultured at 25 °C. Group W comprised shrimp injected with WSSV and maintained at 25 °C continuously. In contrast, Group TW was subjected to a temperature increase to 32 °C at 24 hours post-injection (hpi). Gill samples were collected for analysis 12 hours post-temperature rise (hptr) and subjected to Illumina sequencing (Figure 1A). RNA-seq was used to identify genes responsive to high temperature, particularly those encoding potential transcriptional regulators. Thank you.

(2) The RNA-seq data in Figure 1 focus only on the TFs. The manuscript would benefit from showing all the RNA-seq data and the differentially expressed genes. In particular, are the AMPs upregulated at the same time point? This should not be the case if LvHSF1 were responsible for the transcription of the AMPs, given the time lag between transcription and translation.

Thank you for your suggestion. In Author response image 1, our previous study has revealed that classical heat shock proteins (such as HSP21, HSP70, HSP60, HSP83, HSP90, HSP27, HSP10, and Bip) were induced by RNA-seq between Group TW and Group W, suggesting heat shock proteins exert a crucial role in enhancing the resistance of shrimp to WSSV at elevated temperatures (32 ℃) and underscoring the reliability of our transcriptomic findings (Xiao et al., 2024).

Additionally, we also analyzed the AMPs expression between Group TW and Group W, and the results show that some antimicrobial peptides such as Lysozyme and C-type lectin are upregulated between Group TW and Group W. Notably, we did not detect upregulated expression of SWD between Group TW and Group W. We agree with the reviewer's point of view that there is a time lag between transcription and translation. Supplementary experimental evidences show that the expression level of LvHSF1 is strongly induced by WSSV stimulation, and then the expression level of SWD begins to increase. We have added a description in Lines 136-138 in the revised manuscript.

Author response image 1.

The Figure of the heat shock proteins in Group TW and Group W

Author response image 2.

Transcriptional expression levels of HSF1 and SWD after WSSV stimulation

Reference:

Xiao, B., Wang, Y., He, J., Li, C., 2024. Febrile Temperature Acts through HSP70-Toll4 Signaling to Improve Shrimp Resistance to White Spot Syndrome Virus. J Immunol 213, 1187-1201.

(3) The data showing the tissue distribution of LvHSF1 and nSWD is a rigorous approach and adds to the manuscript. A similar approach to understanding the time course of expression of AMPs in relationship to LvHSF1 expression levels would strengthen the authors' conclusions that LvHSF1 induction in response to high temperatures and viral infection, in turn, upregulates SWD and other antibacterial genes.

Thank you for your suggestion. As you good suggestion, we detected the transcriptional expression levels of HSF1 and SWD after WSSV stimulation for 0, 2, 4, 6, 8, 12, 16, 20, and 24 hours. The transcriptional expression level of SWD was set to 1.00 at 0 h, in the early stage of WSSV infection (0-12 h, except 6 h), the expression level of LvHSF1 is strongly induced, and then the expression level of SWD begins to increase. Theses results show that LvHSF1 induction in response to viral infection, in turn, upregulates SWD and other antibacterial genes. Thank you.

(4) The data (Figures 3 and 4) show that LvHSF1 is necessary to survive WSSV infection at high temperatures but does not affect survival at lower temperatures, even though LvHSF1 limits VP28 levels, and viral load at both temperatures is confusing. Does this suggest that LvHSF1 is not primarily important for protection against the virus but instead, for protection from the heat-induced damage caused by high temperatures, which would not be surprising? The manuscript would benefit if the authors could address this point. How do the authors envision the protection conferred by LvHSF1 only at high temperatures?

Thank you for your comment. Although no significant difference in shrimp survival rates was observed between LvHSF1-silenced shrimp and GFP-silenced shrimp at low temperature (25 °C), shrimp with silenced LvHSF1 exhibited increased viral loads in hemocytes and gills, suggesting that upregulation of HSF1 expression can protect shrimp from WSSV infection.

Notably, the tolerance temperature for L. vannamei growth ranges from 7.5 to 42 °C. When infected with WSSV, shrimp use behavioral fever to elevate their body temperature (~32 °C), thereby inhibiting WSSV infection (Rakhshaninejad et al., 2023; Xiao et al., 2024). And this temperature (~32 °C) will not cause heat-induced damage to the shrimp. Our results demonstrate that febrile temperatures induce HSF1, which in turn upregulates antimicrobial peptides (AMPs) that target viral envelope proteins and inhibit viral replication.

Only at high temperatures, we observed that knockdown of HSF1 did not affect shrimp survival rate (Figure 4A). Thank you again for your valuable feedback.

Reference:

Rakhshaninejad, M., Zheng, L., Nauwynck, H., 2023. Shrimp (Penaeus vannamei) survive white spot syndrome virus infection by behavioral fever. Sci Rep 13, 18034.

Xiao, B., Wang, Y., He, J., Li, C., 2024. Febrile Temperature Acts through HSP70-Toll4 Signaling to Improve Shrimp Resistance to White Spot Syndrome Virus. J Immunol 213, 1187-1201.

(5) Related to the previous comment, the authors do not clearly distinguish between basal effects of LvHSF1 or nSWD induction and heat-induced effects and the differences related to the requirement of LvHSF1 for protection. Simply increasing LvHSF1 levels can result in increased nSWD. SWD levels increase upon WSSV infection even at 25 ℃, and the knockdown experiments suggest that this could also occur through LvHSF1. It would be useful to explicitly differentiate between basal functions of HSF1 and induced functions.

Thank you for your suggestion. In previous responses, we have distinguished between basal effects of LvHSF1 or nSWD induction and heat-induced effects.

As your good suggestion, we injected GST or rHSF1 protein into shrimp, the results showed that recombinant protein HSF1 could significantly induced the expression level of SWD (Supplementary Fig. 5C). Further, after knockdown of SWD, shrimp were injection with rLvHSF1 mixed with WSSV. The results showed that the viral load was significantly lower than the control group 48 hours post WSSV infection (Supplementary Fig. 5D). We have added these results to the Supplementary Figure 5C&5D and added a description in Lines 253-255 and Lines 290-293 in the revised manuscript. Thank you for your constructive comments.

Reviewer #2 (Recommendations for the authors):

(1) Two temperatures are used in the experiments of shrimp. It seems that HSF1 is also upregulated by WSSV infection at 25 ℃. However, this upregulation seems not to be able to protect the animals. The authors compare the infection at 25 and 32 ℃ but did not discuss the findings.

Thank you for your comment. Although no significant difference in shrimp survival rates was observed between LvHSF1-silenced shrimp and GFP-silenced shrimp at low temperature (25 °C), shrimp with silenced LvHSF1 exhibited increased viral loads in hemocytes and gills, suggesting that upregulation of HSF1 expression can protect shrimp from WSSV infection. We have added a discussion of this finding in Lines 461-464 in the revised manuscript. Thank you.

(2) In the abstract the authors say that "These insights provide new avenues for managing viral infections in aquaculture and other settings by leveraging environmental temperature control." However, this point has not been discussed in the main text.

We appreciated your comments. We have added a discussion about the environmental temperature control in Lines 512-514 in the revised manuscript. Thank you.

(3) Line 142: "These results suggest that LvHSF1 may play a key role in enhancing shrimp resistance to WSSV at elevated temperatures." Although this type of conclusion has been made in many studies, I think it is impossible to see a "KEY role" based mainly on change in expression.

Thank you for your suggestion. We have revised this conclusion in the revised manuscript. Thank you.

(4) Section 2.1 Induction of Heat Shock Factor 1 in Response to WSSV at High Temperature

Figure 1. Identification of HSF1 as a key factor induced by high temperature.

The two titles are confusing. Whether the upregulation of HSF1 is a response to high temperature or WSSV infection? I think it is more likely a response to high temperature. Did the authors see the difference in HSF1 expression in shrimp with and without WSSV infection at high temperatures?

Thank you for your comment. We have modified the title of Section 2.1 in the revised manuscript. As your good suggestion, we have measured the expression of LvHSF1 after WSSV challenge at high temperatures (32 ℃) in revised Figure 2F-2H in Line 122 in the revised manuscript. The results demonstrate that the expression of LvHSF1 is strongly induced by WSSV stimulation at high temperatures (32 ℃) in the revised manuscript. Thank you.

(5) Figure 2. Upregulation of LvHSF1 in shrimp challenged by WSSV at both low and high temperatures. Results for WSSV challenge at high temperatures are not included in this figure.

Thank you for your suggestion. As your good suggestion, we have measured the expression of LvHSF1 after Poly (I: C) and WSSV challenge at high temperatures (32 ℃) in revised Figure 2C-2H. The results demonstrate that the expression of LvHSF1 is strongly induced by Poly (I: C) and WSSV stimulation at high temperatures (32 ℃). And we have added a description in Lines 168-179 in revised manuscript. Thank you.

(6) Section 2.2 Expression Profiles of LvHSF1 in Shrimp Under Varied Temperature Conditions and WSSV Challenge. Did the authors try poly IC and WSSV challenge at 32℃, and compare with the un-challenge group? Why were only low temperature was analyzed?

Thank you for your suggestion. As your good suggestion, we have measured the expression of LvHSF1 after Poly (I: C) and WSSV challenge at high temperatures (32 ℃) in revised Figure 2C-2H. And we have added a description about the expression of LvHSF1 after Poly (I: C) and WSSV challenge at high temperatures (32 ℃) in Lines 168-179 in revised manuscript. Thank you.

(7) Figure 2: Please indicate the temperature used in C-E and F-H in the figure legend. Statistical significance: compared with which group? Please provide information in the legend or show it in the bar chart.

Thank you for your suggestion. We have added the description of temperature used in revised Figures 2C-2E. The expression changes of HSF1 were compared with those of PBS control group at the corresponding time and we modified the comparison method of significance in revised Figures 2C-2E. Thank you.

(8) Figure 3H: There are two groups (dsGFP+PBS; dsHSF1+PBS) showing with the same symbol (dot line).

Thank you for your comment. The revised Figure 3H has used different symbols to distinguish the two groups. Thank you.

(9) Line 205: qPCR

Thank you for your careful checks. We have corrected this error in the revised manuscript. Thank you.

(10) Figure 5d and f: Please indicate the sample in each row.

Thank you for your suggestion. We have marked the samples in each row in the revised Figures 5d&5f.

(11) Figure 3 and Figure 4: Why different tissues were analyzed in the two experiments? Low temperature: gill and hemocytes. High temperature: gill and muscle? It is better to use the same tissues so that they can be compared. Please indicate the tissue analyzed in D and d.

Thank you for your suggestion. We have repeated the experiment to detect the copy number of WSSV in hemocyte at high temperature (32 °C) after LvHSF1 knockdown. The results showed that knockdown LvHSF1 showed increased viral loads in shrimp hemocyte (Figure 4C). We have supplemented the tissue information in Figure 4D&4d. Thank you.

(12) Figure 2A The time for temperature treatment? hours or days?

Thank you for your comment. Transcriptional expression of LvHSF1 in different tissues of healthy shrimp subjected to low (25 °C) and high (32 °C) temperatures for 12 hours. We have supplemented this information in the legend of Figure 2A in Lines 840-841 in revised manuscript. Thank you.

(13) Line 249: purified by SDS-PAGE gel?

Thank you for your comment. We have modified this description in Lines 272-274 in current manuscript. Thank you.

(14) Line 258 "Next, to verify whether the anti-WSSV function of nSWD was mediated by LvHSF1 at high temperature". I think it is confusing to use "mediated" here. It seems that HSF1 is downstream of nSWD. Actually, HSF1 controls the expression of nSWD and thus regulates the anti-WSSV effect of shrimp at high temperatures.

We appreciated your comments. We have modified this description in Lines 282-283 in current manuscript. Thank you.

(15) Line 458 "The most probable anti-WSSV mechanism of nSWD is its direct interaction with WSSV envelope proteins VP24 and VP26, potentially inhibiting viral entry into target cells. I suggest the author analyze the entry of WSSV to see whether nSWD blocks this process.

Thank you for your comment. In general, the antimicrobial mechanism of action of AMPs is thought to involve direct membrane disruption, especially for enveloped virus (such as WSSV) (Wilson et al., 2013).

Thanks to the reviewers for their valuable comments. Our manuscript mainly focuses on the febrile temperature-inducible HSF in host antiviral immunity, and the role of HSF1 in regulating antimicrobial effectors (such as SWD). Due to the limitation of the manuscript's length, we will further investigate the functional mechanisms of SWD-specific anti-WSSV in future studies. Thank you.

Reference:

Wilson, S.S., Wiens, M.E., Smith, J.G., 2013. Antiviral Mechanisms of Human Defensins. Journal of Molecular Biology 425, 4965-4980.

(16) Line 435-456 The author discusses the difference between two shrimp species. Did the two studies measure the same immune parameters? I wonder whether the different observation is due to true differences or different methods they used to evaluate the response. If no immune response was promoted in the previous study, what's the possible anti-viral mechanism?

We appreciated your comments. Firstly, the shrimps in the two experimental groups have different adaptability to temperature. The optimal water temperature for M. japonicus growth ranges from 25 to 32 °C, and the tolerance temperature for L. vannamei growth ranges from 7.5 to 42 °C. Secondly, the experimental environmental factors are different in the two experimental groups. Ammonia is a key stress factor in aquatic environments that usually increases the risk of pathogenic diseases in aquatic animals, however, High temperatures (32°C) have been shown to inhibit the replication of WSSV and reduce mortality in WSSV-infected shrimp. Thirdly, the two studies tested different immune indicators. Ammonia-induced Hsf1 suppressed the production and function of MjVago-L, an arthropod interferon analog. In this study, our findings revealed the molecular mechanism through which the HSF-AMPs axis mediates host resistance to viruses induced by febrile temperature. Taken together, the benefits of HSF1 can be attributed to either the host or the pathogen, depending on the nature and context of the host-virus-environment interaction.

(17) Line 472 "directly bind to WSSV envelope proteins and inhibit WSSV proliferation"

I think it is confusing to use "proliferation" here. It seems that the binding of HSF affects the replication process. However, based on the authors' discussion, HSF may likely block viral entry.

Thank you for your suggestion. We have modified this description in Lines 505-507 in the current manuscript. Thank you.

Reviewer #3 (Recommendations for the authors):

In the manuscript titled "Heat Shock Factor Regulation of Antimicrobial Peptides Expression Suggests a Conserved Defense Mechanism Induced by Febrile Temperature in Arthropods", the authors investigate the role of heat shock factor 1 (HSF1) in regulating antimicrobial peptides (AMPs) in response to viral infections, particularly focusing on febrile temperatures. Using shrimp (Litopenaeus vannamei) and Drosophila S2 cells as models, this study shows that HSF1 induces the expression of AMPs, which in turn inhibit viral replication, offering insights into how febrile temperatures enhance immune responses. The study demonstrates that HSF1 binds to heat shock elements (HSE) in AMPs, suggesting a conserved antiviral defense mechanism in arthropods. The findings are informative for understanding innate immunity against viral infections, particularly in aquaculture. However, the logical flow of the paper can be improved. Following are my specific concerns.

Major comments

(1) The study design is pretty good, but the logical flow is not. The following should be improved.

(a) In Figure 1, the reason for selecting HSF1 as the focus of the study is not clearly explained.

Thank you for your comment. In a previous study, we have revealed that heat shock proteins exerted a significant role in enhancing the resistance of shrimp to WSSV at elevated temperature (32 ℃) (Xiao et al., 2024). GO functional enrichment analysis of DEGs between group TW and group W, indicating that most DEGs were involved in biological processes such as protein refolding, chaperone-mediated protein folding, and heat response. Therefore, special attention has been paid to heat shock factor 1 (HSF1), the master regulator of the heat shock response. We have added the description in Lines 136-138 in the revised manuscript. Thank you.

Reference:

Xiao, B., Wang, Y., He, J., Li, C., 2024. Febrile Temperature Acts through HSP70-Toll4 Signaling to Improve Shrimp Resistance to White Spot Syndrome Virus. J Immunol 213, 1187-1201.

(b) As the authors draw models in Figure 9, the established activation mechanism of HSF1 is via trimerization by the release of HSP90, which binds to misfolded proteins under stress conditions, such as heat shock. Therefore, the increase in the HSF1 mRNA level in Figure 1 is strange. The authors need to clarify this issue by explaining this established activation mechanism of HSF1 and also must provide the basis of upregulation of HSF1 by mRNA increase via citing papers in the Introduction.

We appreciated your comments. Under non-stress conditions, HSF monomers are retained in the cytoplasm in a complex with HSP90. During the stress response, such as high temperature, HSF dissociates from the complex, trimerizes, and converts into a DNA-binding conformation through regulatory upstream promoter elements known as heat shock elements (HSEs) (Andrasi et al., 2021). Previous studies have demonstrated that the expression of HSF1 was remarkably induced by stress response, such as high temperature (Ren et al., 2025), virus infection (Merkling et al., 2015), and ammonia stress (Wang et al., 2024). Our results also showed that the expression of LvHSF1 was significant induced by WSSV infection and high temperature (Figure 2). Therefore, this is not surprising that the increase in the HSF1 mRNA level in Figure 1.

In response, we have revised the proposed model to better reflect our experimental findings and the accompanying description. This revision ensures that the schematic is consistent with our data and accurately represents the proposed mechanism. We appreciate your careful review and constructive feedback.

Reference:

Andrasi, N., Pettko-Szandtner, A., Szabados, L., 2021. Diversity of plant heat shock factors: regulation, interactions, and functions. J Exp Bot 72, 1558-1575.

Ren, Q., Li, L., Liu, L., Li, J., Shi, C., Sun, Y., Yao, X., Hou, Z., Xiang, S., 2025. The molecular mechanism of temperature-dependent phase separation of heat shock factor 1. Nature Chemical Biology.

Merkling, S.H., Overheul, G.J., van Mierlo, J.T., Arends, D., Gilissen, C., van Rij, R.P., 2015. The heat shock response restricts virus infection in Drosophila. Sci Rep 5, 12758.

Wang, X.X., Zhang, H., Gao, J., Wang, X.W., 2024. Ammonia stress-induced heat shock factor 1 enhances white spot syndrome virus infection by targeting the interferon-like system in shrimp. mBio 15, e0313623.

(c) For RNA seq analysis in both in Figures 1 and 5, they need to provide changes in conventional HSF1 target chaperones (many HSPs) to validate their RNA seq data.

Thank you for your suggestion. In Authopr response image 1, our previous study has revealed that classical heat shock proteins (such as HSP21, HSP70, HSP60, HSP83, HSP90, HSP27, HSP10, and Bip) were induced by RNA-seq between Group TW and Group W, suggesting heat shock proteins exert a crucial role in enhancing the resistance of shrimp to WSSV at elevated temperatures (32 ℃) and underscoring the reliability of our transcriptomic findings (Xiao et al., 2024). We have added the description in Lines 136-138 in the revised manuscript.

In Figure 5, we have supplemented the heat shock proteins downregulated DEGs by transcriptome sequencing of dsGFP +WSSV (32 ℃) vs. dsLvHSF1 +WSSV (32 ℃) in Supplementary table 2. The results showed that the classical heat shock proteins were downregulated by the RNA-seq, underscoring the reliability of our transcriptomic findings. We have added the description in Lines 213-216 in the revised manuscript. Thank you.

Reference:

Xiao, B., Wang, Y., He, J., Li, C., 2024. Febrile Temperature Acts through HSP70-Toll4 Signaling to Improve Shrimp Resistance to White Spot Syndrome Virus. J Immunol 213, 1187-1201.

(d) In Figure 5, they did experiments by focusing on the changes by HSF1 knockdown at 32 ℃. However, the logical flow should be focusing on genes whose expression was increased by 32 ℃ compared with 25 ℃ (in figure 1), among them they need to characterize HSF1 target genes. Here as mentioned above, classical HSP genes must be included in addition to those AMP genes.

Thank you for your suggestion. As your good suggestion, we have supplemented the heat shock proteins downregulated DEGs by transcriptome sequencing of dsGFP +WSSV (32 ℃) vs. dsLvHSF1 +WSSV (32 ℃) in Supplementary table 2. The results showed that the classical heat shock proteins were downregulated by the RNA-seq, underscoring the reliability of our transcriptomic findings. We have added the description in Lines 213-216 in the revised manuscript. Thank you.

(e) What is the logical basis of just picking nSWD? It is another example of cherry-picking similar to picking HSF1 in Figure 1.

We appreciated your comments. To determine how temperature-induced LvHSF1 restricts WSSV infection, RNA-seq was performed to identify target genes regulated by HSF1. By analyzing the differentially expressed genes (DEGs), we screened eight candidate proteins for immunity-effector molecules, including SWD, CrustinⅠ, C-type lectin, Anti-lipopolysaccharide factor (ALF), and Vago. CrustinⅠ has been shown to play an important role in antiviral immunity (Li et al., 2020); C-type lectin (CTL1) can bind to the VP28, VP26, VP24, VP19, and VP14, thereby inhibiting the infection of WSSV (Zhao et al., 2009); Anti-lipopolysaccharide factor (ALF3) performs its anti-WSSV activity by binding to the envelope protein WSSV189 (Methatham et al., 2017); Vago can inhibit WSSV infection by activating the Jak/Stat pathway in shrimp (Gao et al., 2021). However, the detailed regulatory mechanism of SWD against WSSV was unclear, and particular attention was paid to the SWD. We have added the description in Lines 215-220 in the revised manuscript. Thank you for your valuable comments and the logic of the manuscript has been improved.

Reference:

Li, S., Lv, X., Yu, Y., Zhang, X., Li, F., 2020. Molecular and Functional Diversity of Crustin-Like Genes in the Shrimp Litopenaeus vannamei, Marine Drugs 18, 361.

Zhao, Z.Y., Yin, Z.X., Xu, X.P., Weng, S.P., Rao, X.Y., Dai, Z.X., Luo, Y.W., Yang, G., Li, Z.S., Guan, H.J., Li, S.D., Chan, S.M., Yu, X.Q., He, J.G., 2009. A novel C-type lectin from the shrimp Litopenaeus vannamei possesses anti-white spot syndrome virus activity. Journal of Virology 83, 347-356.

Methatham, T., Boonchuen, P., Jaree, P., Tassanakajon, A., Somboonwiwat, K., 2017. Antiviral action of the antimicrobial peptide ALFPm3 from Penaeus monodon against white spot syndrome virus. Dev Comp Immunol 69, 23-32.

Gao, J., Zhao, B.R., Zhang, H., You, Y.L., Li, F., Wang, X.W., 2021. Interferon functional analog activates antiviral Jak/Stat signaling through integrin in an arthropod. Cell Rep 36, 109761.

(f) Likewise, choosing Atta in S2 cells needs logic.

We appreciated your comments. Our manuscript revealed that febrile temperature inducible HSF1 confers virus resistance by regulating the expression of antimicrobial peptides (AMPs) in L. vannamei. Further, we want to know that whether HSF1 regulation of antimicrobial peptides is a conserved defense mechanism induced by elevated temperature in arthropods, and experiments were performed in an invertebrate model system (Drosophila S2 cells). Previous study showed that DmAMPs (such as Attacin A, Cecropins A, Defensin, Metchnikowin, and Drosomycin) exerted a significant role in the antiviral immunity in Drosophila (Zhu et al., 2013). Our results showed that the expression of Attacin A, Cecropins A and Defensin were remarkably induced by DmHSF, and the expression of Attacin A was the highest induced. Therefore, DmAtta was chosen as a representative to further demonstrate that DmHSF1 exerts its anti-DCV function by regulating DmAMPs. We have added the description in Lines 328-330 and Lines 361-364 in the revised manuscript. Thank you for your valuable comments and the logic of the manuscript has been improved.

Reference:

Zhu, F., Ding, H., Zhu, B., 2013. Transcriptional profiling of Drosophila S2 cells in early response to Drosophila C virus. Virol J 10, 210.

(2) From Figure 6I to 6K, the authors aimed to verify whether the anti-WSSV function of nSWD was mediated by LvHSF1 at high temperatures. However, what they showed was just showing that nSWD plays anti-WSSV function downstream of HSF1. The authors should show additional data for dsControl+rnSWD.

Thank you for your suggestion. As your suggestion, after knockdown of SWD, shrimp were injection with rLvHSF1 mixed with WSSV. The results showed that the viral load was significantly lower than the control group 48 hours post WSSV infection (Supplementary Fig. 5D). We have added these results to the Supplementary Figure 5C&5D and added a description in Lines 290-293 in the revised manuscript. Thank you for your constructive comments.

(3) For the physical interaction between nSWD and WSSV, it will be great if the authors perform Alphafold3 prediction analysis (Abramson et al PMID: 38718835).

Thank you for your suggestion. As you suggestion, we performed Alphafold3 prediction analysis on SWD and WSSV (VP24 and VP26). The predicted template modeling (pTM) score measures the accuracy of the entire structure. A pTM score above 0.5 means the overall predicted fold for the complex might be similar to the true structure. The Alphafold3 prediction results show that there is a possible interaction between SWD and WSSV. Notably, our manuscript demonstrated that rSWD could interact with VP24 and VP26 by pulldown assays and confocal analysis.

Author response image 3.

Alphafold3 prediction analysis of SWD&VP24 as follow (pTM = 0.64)

Author response image 4.

Alphafold3 prediction analysis of SWD&VP26 as follow (pTM = 0.53)

Minor comments

(1) In the Abstract and many other places, the authors need to specifically write "Drosophila S2 cells" instead of "Drosophila" because conventionally Drosophila implies fruit fly as an organism. We don't say cultured human cells as "human" or "Homo sapiens" in papers.

Thank you for your suggestion. We have modified the description of Drosophila in the revised manuscript. Thank you.

(2) Figure numbers can be reduced for better readability. I would combine Figures 1 and 2, and Figures 3 and 4. If the combined figures are too crowded, some can go to into supplementary figures.

Thank you for your suggestion. We have moved the Poly (I: C) data to Supplementary Figure 2 in the revised manuscript. However, we have added some experimental data to Figures 1, 2, 3, and 4. Therefore, we did not combine Figure 1 and Figure 2, and Figures 3 and 4. Thank you.

(3) One of the best-understood roles of HSF1 in physiology other than heat shock response is longevity, in particular with C. elegans. The authors need to mention this in the Discussion by citing the following recent review paper (Lee PMID: 36380728).

Thank you for your suggestion. We have supplemented the description of HSF1 regulating longevity and aging of organisms and cited the above reference in the revised manuscript (Lee and Lee, 2022). Thank you.

Reference:

Lee, H., Lee, S.V., 2022. Recent Progress in Regulation of Aging by Insulin/IGF-1 Signaling in Caenorhabditis elegans. Mol Cells 45, 763-770.

(4) Please make your own label for small letter panels or transfer small letter panels to supplementary figures.

Thank you for your suggestion. We have adjusted the relevant letter labels. The uppercase letters represent the main image of the Figure, and the small letter panels are the corresponding supplementary instructions in the revised manuscript. Thank you.

(5) In the introduction part, I recommend changing the references for HSFs and HSR with recent ones.

Thank you for your suggestion. We have added the latest references for HSFs and HSR in the Introduction part of the revised manuscript. Thank you.

(6) In Figure 1, it is not intuitive to understand the name groups W and TW.

We appreciated your comments. We have added the description of Group W and Group TW in revised Figure 1. Group W comprised shrimp injected with WSSV and maintained at 25 °C continuously. In contrast, Group TW was subjected to a temperature increase to 32 °C at 24 hours post-injection (hpi). Gill samples were collected for analysis 12 hours post-temperature rise (hptr) and subjected to Illumina sequencing. Thank you.

(7) Please add some kinds of sequence comparisons of SWD and nSWD for readers to understand the homology.

We appreciated your comments. We have added the multiple sequence alignment of SWD proteins in shrimp species in revised Supplementary Figure 3. Highly conserved amino acid residues and cysteine and residues are highlighted in red, indicating that LvSWD is a conserved antimicrobial peptide of the Crustin family. Thank you.

(8) Naming nSWD with "newly identified" is strange as it will not be new anymore as time goes by. Please change the name.

Thank you for your suggestion. We have modified the name of nSWD to SWD in the revised manuscript. Thank you.

(9) Please write the full name for Lv (Litopenaeus vannamei), Dm (Drosophila melanogaster), ds (double-stranded) before using LvHSF1, DmHSF1, and dsLvHSF1.

Thank you for your comments. We have added the full name of LvHSF1, DmHSF1, and dsLvHSF1 in the revised manuscript. Thank you.

(10) In Figure 2, it will be better to transfer poly I:C data to supplementary figures.

Thank you for your comments. We have moved the Poly (I: C) data to Supplementary Figure 2 in the revised manuscript. Thank you.

(11) The label for pGL3-nSWD-M12 is confusing. M1 and M2 are OK. Please change M12 with M1/2 or another one.

Thank you for your suggestion. We have changed pGL3-nSWD-M12 with pGL3-nSWD-M1/2 in the revised manuscript. Thank you.

Author Response:

The following is the authors’ response to the previous reviews

eLife Assessment

This article presents useful findings on how the timing of cooling affects the timing of autumn bud set in European beech saplings. The study leverages extensive experimental data and provides an interesting conceptual framework for the various ways in which warming can affect but set timing. The statistical analysis is compelling, but indicates some factors that may temper the authors' claims, while the designs of experiments offer incomplete support for the current claims as they rely on one population under extreme conditions for only one year each while a confounding effect (time in a chamber) sometimes lacks a control.

We thank the editor and reviewers for their consideration of our revised manuscript and for their constructive suggestions. In response to the editor’s guidance, we have ensured that: 1) the experimental design is clearly presented as physiological forcing, 2) the Solstice-as-Phenology-Switch concept is explicitly defined, limited, and framed as inferred, 3) conclusions are strictly aligned with the scope of the evidence, and limitations are acknowledged transparently.

We hope these revisions fully address the remaining concerns and clarify both the conceptual framework and the appropriate scope of inference.

Public Review:

Reviewer #1 (Public review):

The authors identified the summer solstice (June 21) as a phenological "switch point", but the flexibility of this switch point remains poorly understood. A more precise explanation of what "flexibility" means in this context is needed, along with a description of the specific experimental results that would demonstrate this flexibility.

We agree that the concept of “flexibility” required clearer definition and a more explicit link to the experimental results. In the Introduction, we now explicitly define flexibility as the capacity for the effective timing of the phenological switch to shift earlier or later depending on developmental progression, rather than occurring at a fixed calendar date. This switch occurs at the compensatory point between the antagonistic influences of early-season development [ESD effect] and late-season temperature [LST effect](L92-98). We have extended and clarified our explanation of the summer solstice’s role in this framework (L69-90). We propose that the solstice acts as an environmental switch that initiates the LST effect, as declining daylengths signal trees to become responsive to late-season cooling (L92-94). The compensatory point then occurs where the advancing ESD effect is balanced by the delaying LST effect. This point should therefore not be fixed to a calendar date but instead vary with developmental progression each year (L75-95).

In the Discussion, we clarify that flexibility is demonstrated experimentally by the observation that the magnitude of July cooling effects (LST effect) on autumn phenology depend on prior developmental rate (ESD effect) [3.4 times greater delay in late-leafing trees], indicating that the position of the compensatory point is development-dependent rather than fixed to June 21 (L398-410). We have made consistent edits throughout the Discussion, in particular in the ‘Support for the Solstice-as-Phenology-Switch Hypothesis’ subsection (L514-530).

The experiment did not directly measure the specific date of the phenological switch point. Instead, it was inferred by comparing temperature effects before and after the solstice. The manuscript should clearly state that this switch point remains an inferred conceptual node rather than a directly measured variable.

We fully agree and have clarified this in the revised manuscript. In the Discussion, we now clearly state that the compensatory point is a conceptual node inferred from responses to cooling before the solstice (June), directly after it (July), or later in the growing season (August) rather than a directly observed phenological event (L352-358 & L405-406).

In Experiment 1, the effect of bud type (terminal vs. lateral) was inconsistent across the overall model and the different leafing groups. The authors should provide a more thorough discussion of potential reasons for this inconsistency.

This inconsistency reflects biological complexity. In the Discussion, we now expand our interpretation to note that terminal and lateral buds may differ in developmental status, resource allocation and hormonal context. We emphasize that bud-type effects are therefore expected to be context-dependent and to interact with wholeplant developmental state, which plausibly explains why effects differ across leafing groups and models (L390-396).

In addition, the statistical model for Experiment 1 indicates that the measured variables (summer cooling and leaf emergence date) explain only 23.4% of the variation in bud formation timing. This leaves over 76% of the variation unexplained, suggesting that other important factors are involved. The discussion should address this limitation in greater depth, moving beyond a focus on the measured variables.

We now discuss the explained and unexplained variance in more detail. We also make it clear that our experiment was designed to test specific mechanistic pathways rather than to fully explain all phenological variability or maximise predictive power L417-419).

In the Discussion, we acknowledge that a substantial fraction of variation remains unexplained (L419-421). We discuss the possibility of other physiological mechanisms, such as photosynthetic assimilation, contributing to the unexplained variation (L421-427). However, large inter-individual variability is commonplace in autumn phenology. A low intra-class correlation coefficient (ICC = 0.26; see L276-280 for methods) suggests much of the remaining variation is attributable to individual-level differences rather than missing explanatory variables (L429-431). In line with the literature, we suggest that genetic and epigenetic differences likely contributed significantly to inter-individual variation, even within a single provenance population (L431-434). In this context of high individual variability, leaf-out timing (ESD effect) and summer cooling treatment (LST effect) together explaining 23.4% of variation in bud set timing is biologically meaningful and demonstrates the mechanistic importance of these processes (L438-441). For completeness, we also briefly discuss alternate sources of within-treatment variability (L434-437).

Reviewer #2 (Public review):

I think the experiments are interesting, but I found the exact methods of them somewhat extreme compared to how the authors present them.

We appreciate this concern and have substantially revised the manuscript to clarify the experimental logic. In the Introduction, we now state explicitly that the study uses temperature regimes that were designed as strong physiological forcing treatments, intended to deeply constrain development and isolate mechanisms rather than to simulate natural or future climatic conditions (L113-115).

In the Methods, we have enhanced our description of the non-linear effects of temperatures below 10°C on physiological processes (L154-158).

At the start of the Discussion, we have added a dedicated paragraph clarifying the scope of inference: the experiment tests causality and constraint (i.e. whether specific physiological processes can drive phenological shifts), not quantitative responses under realistic climate scenarios (L346-363). Throughout the Discussion, we have revised language that could be read as scenario-based interpretation, replacing it with mechanistic phrasing.

Further, given that much of the experiment happened outside, I am not sure how much we can generalize from one year for each experiment, especially when conducted on one population of one species.

Given the large individual variation expected in phenological experiments, we used single experimental populations of single provenance beech saplings to minimise uncontrolled for variation arising from genetic differences (L358-360). This allowed us to elucidate mechanisms despite noisy biological heterogeneity associated with phenology.

In the last round of revision, we toned down statements of generalisation. In the Discussion, we now go further to clarify what mechanistic understanding can be gleamed directly from our findings and then cautiously make suggestions how these mechanisms may play out in natural systems. We repeatedly state the intention of the study as mechanistic inference rather than predictive power, e.g. “However, extrapolations to more complex natural ecosystems should be made with caution as our experimental design prioritised mechanistic inference over generalisability and predictive power.” (L417-419). Alongside our previous calls for tests on other species, we now additionally call for tests on other provenances of beech (L511-512).

I was also very concerned by the revisions.

If this concern stems from the confusion regarding line-numbers and the two submitted versions of the manuscript (with tracked changes and without tracked changes; as required by eLife), then we hope that situation is now clarified. Otherwise, the authors do not understand why our previous revisions would be perceived as being concerning. Regardless, we have made every attempt to address the remaining comments comprehensively.

Further, I am at a loss about their hypothesis, when they write in their letter: "Importantly, the Solstice-asPhenology-Switch hypothesis does not assume that the reversal is fixed to June 21." Why on earth reference the solstice if the authors do not mean to exactly reference the solstice?

We appreciate this important conceptual point. The Solstice-as-Phenology-Switch hypothesis is central to our conceptual model and therefore requires clear explanation. In concert with our changes in response to Reviewer 1’s comment regarding flexibility, we have substantially revised and improved our description of this hypothesis (L69-108).

Whilst the summer solstice is fixed to a calendar date (June 21), the timing of when trees change their autumn phenological responses to temperature is not (L88-90 & L515-517). This occurs when the compensatory point of two antagonistic effects is crossed. Higher early-season development rates (which are driven by temperature) have an advancing (negative) effect on autumn phenology, which we now refer to as the ESD effect (L71-78). Warmer late-season temperatures have a delaying (positive) effect because trees become phenologically susceptible to cooling, i.e. overwintering responses are induced in response to cooling, which we now refer to as the LST effect (L78-82). The point in time when these two effects balance each other out, i.e. the net effect = 0, is the compensatory point (L95-97 & L523-525). The reason this point occurs after the solstice, is because the LST effect only becomes active when days begin to shorten (L92-94 & L522-523). The solstice acts as an environmental switch, initiating trees’ susceptibility to cooling. Therefore, the solstice is referenced in the hypothesis because it forms a daylength barrier. In this framework, the compensatory point cannot occur earlier than the solstice because day lengths are still increasing (L517-519).

In the Introduction and Discussion, we clarify that the solstice is referenced as a biologically meaningful photoperiodic cue, not as a fixed threshold date. We now emphasise that the hypothesis concerns a seasonal reversal in responses to temperature structured around photoperiod, whose effective timing depends on developmental state, rather than a reversal occurring precisely on June 21. To avoid confusion, we have reworded phrases such as “summer solstice effect reversal” to “reversal of phenological responses to temperature after the summer solstice” (L371). In accordance, we have also changed the title to “Developmental constraints mediate the reversal of temperature effects on the autumn phenology of European beech after the summer solstice”.

The following comments stem from the first round of review. We have previously revised the manuscript in accordance with these comments. For most of these points we do not see further cause for changes except for any overlap with comments above. We therefore predominantly copy our previous responses in quotes for clarity, the exception being the comment regarding the framing of our results in relation to natural systems.

The comments below relate to my original review with many of them still applying.

Methods: As I read the Results I was surprised the authors did not give more info on the methods here. For example, they refer to the 'effect of July cooling' but never say what the cooling was. Once I read the methods I feared they were burying this as the methods feel quite extreme given the framing of the paper.

“We understand the concern regarding the structure of the manuscript and note that the methods section was moved to the end of the paper in accordance with eLife’s recommended formatting. We have now moved the methods section before the results to ensure that readers are familiar with the treatments before encountering the outcomes.

Regarding presentation, treatment details are now described in both the Methods and the relevant figure legends. Given this structure, we have chosen not to restate the full treatment conditions in the main Results text to avoid repetition.”

The paper is framed as explaining observational results of natural systems, but the treatments are not natural for any system in Europe of which I have worked in. For example a low of 2 deg C at night and 7 deg C during the day through end of May and then 7/13 deg C in July is extreme. I think these methods need to be clearly laid out for the reader so they can judge what to make of the experiment before they see the results.

We appreciate the reviewer’s concern regarding the use of relatively extreme temperature treatments and the need to ensure that our conclusions are consistent with the motivation for using them. The manuscript was also revised in this regard in the previous round, and we copy the relevant responses at the bottom of this response. Despite this, we agree that further explanation of how our experimental treatments suited the aims of our study was still required.

The aim of these treatments was not to reproduce typical ambient conditions, but to act as a mechanistic probe. Such mechanisms are not readily identifiable from observations or mild manipulations, because the expected effects are small relative to natural variability; stronger perturbations are therefore required to generate a diagnostic contrast. By strongly constraining development in the early-season, and by providing a robust cooling signal in the late-season, we sought to reveal the causal structure underlying the observed solstice-related reversal in temperature effects on autumn phenology.

Temperatures below 10°C intensively slow down cell division and mitotic rates, these rates then rapidly and non-linearly approach 0 as temperatures drop towards 0°C (Körner, 2021). As reflected in L152-158 of the revised manuscript, we selected a spring cooling regime of 2–7 °C to strongly slow developmental processes while maintaining a clear thermal safety margin that eliminates the risk of frost damage. Although a milder cooling regime (e.g. 5–10 °C) would be less extreme, it would also be expected to produce only a comparatively small reduction in developmental rates, thereby substantially reducing our ability to generate distinct early- and late-developing individuals and to detect carry-over effects on autumn phenology. Applying strong cooling therefore increases signal-to-noise and allows us to detect the underlying mechanism, which would not be possible with temperature treatments that represent average contemporary climatic variation.

The use of conditions out with the norm is a standard practice to elucidate mechanisms in ecology, where organisms are often pushed to their physiological limits or transplanted into environments fundamentally different to those which they are adapted (Somero, 2010; Berend et al., 2019). Experiments targeting autumn phenology have utilised a broad range of environmental conditions from moderate to extreme manipulations (Tanino et al., 2010). For example, to test the controls of growth cessation and dormancy induction in Prunus species, one study applied a range of treatments including constant 9°C temperature and 24 hour photoperiod between April and July (Heide, 2008).

Our experimental design aimed to reduce rates of development, cell division and maturation. In the Methods, we describe this aim and clearly state that the experimental design was not intended to mimic natural climatic variation (L154-156 & L181-186). Importantly, our conclusions are framed at the level of direction, timing, and interaction of effects, rather than the magnitude expected under contemporary or future field conditions (L360-363).

This framing intends to reflect the primary inference of this study, which concerns when and why temperature effects reverse around the solstice, and how this timing depends on developmental state and diel temperature exposure, rather than making quantitative predictions for present-day or future climates. This aligns our conclusions with the experimental design. We have further revised the Discussion to explain these aims and conclusions more clearly, including the addition of a subsection at the beginning titled “Experimental forcing and scope of inference” (L346-363). We have also set up this expectation in the Introduction (L113-115).

Additionally, we have improved the Discussion in a number of related aspects.

We explicitly separate mechanistic conclusions and any relation to natural systems, remaining cautious to not overgeneralise or overstate our findings (L417-419).

We now include a dedicated paragraph explaining that, although these specific conditions are not likely to be found in beech’s range, analogous developmental constraints can arise during cold springs, late cold spells following budburst, or at high-elevation and continental sites where temperatures remain low despite increasing photoperiod (L540-545, L583-588). We further explain that because developmental progression integrates temperature cumulatively over time, even short episodes of strong cooling can exert lasting carry-over effects on seasonal timing, thereby linking the forced experimental responses to processes relevant under natural, fluctuating conditions (L545-550).

We explicitly state that the decoupling of day and night temperatures was not intended to represent realistic meteorological states (L458-460). We explain that this design was used diagnostically to isolate inherently diel physiological processes (e.g. nocturnal growth, cell division and expansion versus daytime carbon assimilation), and that the observed responses demonstrate the importance of diel timing of temperature exposure rather than the realism of the imposed cycles (L460-468).

Previous response:

We recognise that our temperature treatments were severe and do not mimic real world scenarios. They were deliberately designed to create large contrasts in developmental rates, thereby maximising our ability to detect the mechanisms underpinning the solstice switch. For example, the severe cooling between 4 April and 24 May was specifically designed to slow spring development as much as possible without damaging the plants. We have added text in the Methods to clarify this aim.

I also think the control is confounded with growth chamber experience in Experiment 1. That is, the control plants never experience any time in a chamber, but all the treatments include significant time in a chamber. The authors mention how detrimental chamber time can be to saplings (indeed, they mention an aphid problem in experiment 2) so I think they need to be more upfront about this. The study is still very valuable, but -- again -- we may need to be more cautious in how much we infer from the results.

We appreciate the reviewer’s concern about the potential confounding effect of chamber exposure in experiment 1. We have now discussed this limitation more explicitly, adding further explanation to the Methods and Discussion.

Note that chamber-related problems (e.g. aphid infestations) primarily occurred under warm chamber conditions, whereas our experiment 1 cooling treatments maintained low temperatures that suppressed such issues. This means that an equivalent “warm chamber control” could have been associated with its own artefacts, as trees kept under warm chamber conditions would have been exposed to additional stressors that were not present under natural growing conditions. To address this point, we included a chamber control in experiment 2. While aphid abundance was indeed higher in the warm chamber controls, chamber exposure itself had no detectable effect on autumn phenology. This suggests that the main findings of experiment 1 are unlikely to be artefacts of chamber conditions.

Nevertheless, we agree that chamber exposure remains a potential limitation of experiment 1, which requires clear acknowledgement. We now state this more explicitly in the manuscript while also emphasising that our results are supported by experiment 2 and by converging lines of external evidence.

Also, I suggest the authors add a figure to explain their experiments as they are very hard to follow. Perhaps this could be added to Figure 1?

We have now added figures to the methods section to depict the experimental timelines and settings more clearly (Figs. 2 and 3).

Finally, given how much the authors extrapolate to carbon and forests, I would have liked to see some metrics related to carbon assimilation, versus just information on timing.

We agree that carbon assimilation is an important component of forest carbon dynamics. However, the primary aim of this study was to identify how developmental state and diel cycles mediate temperature effects on autumn phenology, rather than to quantify carbon assimilation per se. Assessing photosynthetic controls on autumn phenology would require a substantially different experimental design and is therefore beyond the scope of the present study.

That said, we were able to include measurements of photosynthetic assimilation during pre-solstice cooling (now presented as Fig. S12 for all treatments). These data show that cooling strongly reduced assimilation across all treatments, despite their markedly different phenological outcomes. This supports our interpretation that variation in assimilation alone cannot explain the observed phenological responses, consistent with previous manipulative and observational studies reporting a weak role of late-season assimilation in controlling autumn phenology.

Fagus sylvatica: Fagus sylvatica is an extremely important tree to European forests, but it also has outlier responses to photoperiod and other cues (and leafs out very late) so using just this species to then state 'our results likely are generalisable across temperate tree species' seems questionable at best.

We agree that Fagus sylvatica has a stronger photoperiod dependence than many other European tree species. As we note in our response to Reviewer 1, our findings align with previous research across temperate northern forests. Within our framework, interspecific variation in leaf-out timing would not alter the overall response pattern, though it could shift the specific timing of effect reversals. For example, earlier-leafing species may approach completion of development sooner and thus show sensitivity to late-season cooling earlier than F. sylvatica. Nevertheless, we acknowledge the importance of not overstating generality. We have therefore revised the manuscript to phrase conclusions more cautiously and highlight the need for further research across species.

And the referenced response to Reviewer one:

We agree that extrapolation from our experiments on Fagus sylvatica to other species and natural forests requires caution. However, it is precisely the controlled nature of our design that allowed us to isolate the precise mechanisms that appear to underpin the solstice switch, highlighting the role of diel and seasonal temperature variation. In natural systems, additional variables such as competition, precipitation, and soil heterogeneity can strongly influence phenology, but they also make it difficult to disentangle causal mechanisms. By minimising these confounding factors, our experiment provided a clear test of how temperature before and after the solstice regulates growth cessation.

To acknowledge the limitation, we have toned down statements about generalisation (e.g. “likely generalisable” to “other temperate tree species may display similarities”) and explicitly call for follow-up studies across species and forest contexts. At the same time, we highlight that our findings align with independent evidence from manipulative experiments, satellite observations, flux measurements, and groundbased phenology, which suggests the mechanisms we report may extend beyond the specific populations studied here.”

As described in responses above, we have further clarified what can be directly concluded from our study, avoiding overgeneralisation.

Measuring end of season (EOS): It's well known that different parts of plants shut down at different times and each metric of end of season -- budset, end of radial expansion, leaf coloring etc. -- relate to different things. Thus I was surprised that the authors ignore all this complexity and seem to equate leaf coloring with budset (which can happen MONTHS before leaf coloring often) and with other metrics. The paper needs a much better connection to the physiology of end of season and a better explanation for the focus on budset. Relatedly, I was surprised the authors cite almost none of the literature on budset, which generally suggests is it is heavily controlled by photoperiod and population-level differences in photoperiod cues, meaning results may different with a different population of plants. 

We thank the reviewer for pointing out that our discussion of the responses of different EOS metrics needs more clarity. We agree with much of this perspective, and we have added an additional analysis of leaf chlorophyll content data to use leaf discolouration as an alternative EOS marker. On this we would like to make two important points:

Firstly, we agree that bud set often occurs before leaf discolouration, although this can depend on which definition of leaf discolouration is used. In experiment 1, budset occurred on average on day-of-year (DOY) 262 and leaf senescence (50% loss of leaf chlorophyll) occurred on DOY 320. However, we do not necessarily agree that this excludes the combined discussion of bud set and leaf senescence timing. Whilst environmental drivers can affect parts of plants differently, often responses from different end-of-season indicators (e.g. bud set and loss of leaf chlorophyll) are similar, even if only directionally. Figure S11 shows how, across both experiments, treatment effects were tightly conserved (R² = 0.49) amongst the two phenometrics. In accordance with these revisions, we have updated the manuscript title to “Developmental constraints mediate the summer solstice reversal of climate effects on the autumn phenology of European beech”.

Secondly, shifts in bud set timing remain the primary focus of the manuscript as these shifts are of direct physiological relevance to plant development and dormancy induction, whereas leaf discolouration may simply follow bud set as a symptom of developmental completion. This is supported by our results, which show stronger responses of bud set than leaf senescence (Figs. 4 & 5 vs. Figs. S9 & S10).

Following the reviewer’s suggestion, we have included more references on the topic of bud set and its environmental controls. The reviewer rightly stresses that photoperiod is considered the most important factor. Photoperiod is therefore key in our conceptual model. However, the responses we observed in F. sylvatica cannot be explained by photoperiod alone. For example, in experiment 1, July cooling delayed the autumn phenology of late-leafing trees but had negligible impact on early-leafing trees, even though both experienced the exact same photoperiod. Moreover, in experiment 2, day, night and full-day cooling showed substantial variations in their effects despite equal photoperiod across the climate regimes. This is why we suggest that the annual progression of photoperiod modulates the responses to temperature variations instead of eliciting complete control.

Following the addition of an analysis of leaf senescence data, we also revised the terminology in places (including the title) from “primary growth cessation/bud set” to the broader term “autumn phenology.” This term is intended to encompass two distinct but related physiological processes—bud set and leaf senescence—both of which are commonly used as markers of autumn phenology and the end of the growing season.

Somewhat minor comments:

(1) How can a bud type -- which is apical or lateral -- be a random effect? The model needs to try to estimate a variance for each random effect so doing this for n=2 is quite odd to me. I think the authors should also report the results with bud type as fixed, or report the bud types separately.

We have revised the analysis to include bud type as a fixed effect. There are only very minor numerical adjustments (e.g. rounding to 4.8 days instead of 4.9) and inferences are not altered. We also report the bud type effects for experiment 1 and experiment 2.

(2) I didn't fully see how the authors results support the Solstice as Switch hypothesis, since what timing mattered seemed to depend on the timing of treatment and was not clearly related to solstice. Could it be that these results suggest the Solstice as Switch hypothesis is actually not well supported (e.g., line 135) and instead suggest that the pattern of climate in the summer months affects end of season timing?

Our responses to the main comments in this new round of revision have comprehensively covered this topic.

References

Berend K, Haynes K, MacKenzie CM. 2019. Common garden experiments as a dynamic tool for ecological studies of alpine plants and communities in northeastern North America. Rhodora 121: 174.

Heide OM. 2008. Interaction of photoperiod and temperature in the control of growth and dormancy of Prunus species. Scientia Horticulturae 115: 309–314.

Körner C. 2021. Alpine Plant Life: Functional Plant Ecology of High Mountain Ecosystems. Cham: Springer International Publishing.

Somero GN. 2010. The physiology of climate change: how potentials for acclimatization and genetic adaptation will determine ‘winners’ and ‘losers’. Journal of Experimental Biology 213: 912–920.

Tanino KK, Kalcsits L, Silim S, Kendall E, Gray GR. 2010. Temperature-driven plasticity in growth cessation and dormancy development in deciduous woody plants: a working hypothesis suggesting how molecular and cellular function is affected by temperature during dormancy induction. Plant Molecular Biology 73: 49–65.

Author response:

The following is the authors’ response to the original reviews

eLife Assessment

This valuable study combined careful computational modeling, a large patient sample, and replication in an independent general population sample to provide a computational account of a difference in risk-taking between people who have attempted suicide and those who have not. It is proposed that this difference reflects a general change in the approach to risky (high-reward) options and a lower emotional response to certain rewards. Evidence for the specificity of the effect to suicide, however, is incomplete, which would require additional analyses.

We thank the editors and reviewers for this important assessment. Based on clinical interviews, we included patients with and without suicidality (S⁺ and S^- groups). However, in line with suicidal-related literature (e.g., Tsypes et al., 2024), two groups also differed substantially in the severity of symptoms (see Table 1). To address the request for evidence on specificity to suicidality beyond general symptom severity, we performed separate linear regressions to explain in gambling behaviour, value-insensitive approach parameter (β_gain), and mood sensitivity to certain rewards (β_CR) with group as a predictor (1 for S⁺ group and 0 for S^- group) and scores for anxiety and depression as covariates. Results remained significant after controlling anxiety and depression (ps < 0.027; Table S8). Given high correlations among anxiety and depression questionnaires (rs > 0.753, ps < 0.001), we performed Principal Components Analysis (PCA) on the clinical questionnaire to extract the orthogonal components, where each component explained 86.95%, 7.09%, 3.27%, and 2.68% variance, respectively. We then performed linear regressions using these components as covariates to control for anxiety and depression. Our main results remained significant (ps < 0.027; Table S9). We believe that these analyses provide evidence that the main effects on gambling and on mood were specific to suicide.

Moreover, as Reviewer 3 pointed out, these “absence of evidence” cannot provide insights of “evidence of absence”. Although we median-split patients by the scores of general symptoms (e.g., depression and anxiety-related questionnaires) and verified no significant differences in these severities (Figure S11), we additionally conducted Bayesian statistics in gambling behavior, value-insensitive approach parameter, and mood sensitivity to certain rewards. BF₀₁ is a Bayes factor comparing the null model (M₀) to the alternative model (M₁), where M₀ assumes no group difference. BF₀₁ > 1 indicates that evidence favors M₀. As can be seen in Table S7, most results supported null hypothesis, suggesting that general symptoms of anxiety and depression overall did not influence our main results. Overall, we believe that these analyses provide compelling evidence for the specificity of the effect to suicide, above and beyond depression and anxiety.

Beyond these specific findings, this work highlights the broader utility of computational modelling and mood to better understand behavioral effect, showing how to use both mood and choice data to better comprehend a psychiatric issue. 

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors use a gambling task with momentary mood ratings from Rutledge et al. and compare computational models of choice and mood to identify markers of decisional and affective impairments underlying risk-prone behavior in adolescents with suicidal thoughts and behaviors (STB). The results show that adolescents with STB show enhanced gambling behavior (choosing the gamble rather than the sure amount), and this is driven by a bias towards the largest possible win rather than insensitivity to possible losses. Moreover, this group shows a diminished effect of receiving a certain reward (in the non-gambling trials) on mood. The results were replicated in an undifferentiated online sample where participants were divided into groups with or without STB based on their self-report of suicidal ideation on one question in the Beck Depression Inventory self-report instrument. The authors suggest, therefore, that adolescents with decreased sensitivity to certain rewards may need to be monitored more closely for STB due to their increased propensity to take risky decisions aimed at (expected) gains (such as relief from an unbearable situation through suicide), regardless of the potential losses.

Strengths:

(1) The study uses a previously validated task design and replicates previously found results through well-explained model-free and model-based analyses.

(2) Sampling choice is optimal, with adolescents at high risk; an ideal cohort to target early preventative diagnoses and treatments for suicide.

(3) Replication of the results in an online cohort increases confidence in the findings.

(4) The models considered for comparison are thorough and well-motivated. The chosen models allow for teasing apart which decision and mood sensitivity parameters relate to risky decision-making across groups based on their hypotheses.

(5) Novel finding of mood (in)sensitivity to non-risky rewards and its relationship with risk behavior in STB.

Weaknesses:

(1) The sample size of 25 for the S- group was justified based on previous studies (lines 181-183); however, all three papers cited mention that their sample was low powered as a study limitation.

We thank the Reviewer for rising this concern. We agree that the sample size for S^- group (n=25) is modest, and the prior studies we cited also acknowledged limited power. We wanted to point out that we obtained a comparable sample size to a prior study. In the revision, we therefore updated the section to justify this sample size in which we acknowledge the limited power of our study in the limitation section. Please see our clarification below:

Page 32:

“Third, despite replicating our main results in an independent dataset (n=747), the modest S^- subgroup size (n=25) has a limited statistical power.”

(2) Modeling in the mediation analysis focused on predicting risk behavior in this task from the model-derived bias for gains and suicidal symptom scores. However, the prediction of clinical interest is of suicidal behaviors from task parameters/behavior - as a psychiatrist or psychologist, I would want to use this task to potentially determine who is at higher risk of attempting suicide and therefore needs to be more closely watched rather than the other way around (predicting behavior in the task from their symptom profile). Unfortunately, the analyses presented do not show that this prediction can be made using the current task. I was left wondering: is there a correlation between beta_gain and STB? It is also important to test for the same relationships between task parameters and behavior in the healthy control group, or to clarify that the recommendations for potential clinical relevance of these findings apply exclusively to people with a diagnosis of depression or anxiety disorder. Indeed, in line 672, the authors claim their results provide "computational markers for general suicidal tendency among adolescents", but this was not shown here, as there were no models predicting STB within patient groups or across patients and healthy controls.

Thank you for these thoughtful comments. Our study focuses on why adolescent patients with suicidality have increased risk behavior, aiming to provide a mechanism-based target for suicide prevention. Therefore, our dependent variable in the mediation model was gambling behavior. We also agree that the clinically relevant question is whether suicidality can be predicted from task-derived behavior/parameters. We thus used risky behavior and the potential mental parameters to predict STB. Linear regressions showed that gambling behavior, as well as the value-insensitive approach parameter, can predict suicidal symptom scores among patients (former: β = 9.189, t = 2.004, p = 0.048; latter: β = 5.587, t = 2.890, p = 0.005). In healthy controls, these predictions failed (gambling behavior: β = 1.471, t = 0.825, p = 0.411; approach: β = 0.874, t = 1.178, p = 0.241). These results suggest that clinical relevance of these findings apply exclusively to people with a diagnosis of depression or anxiety disorder. We found same patterns for the mood parameter (mood sensitivity to certain rewards: patients: β = -28.706, t = -2.801, p = 0.006; healthy controls: β = -2.204, t = -0.528, p = 0.599). In sum, we believe that our statement of “computational markers for general suicidal tendency among adolescents” is reasonable now. Please see our revisions below:

Page 17:

“Furthermore, linear regression showed that gambling rate can predict the current suicidal ideation score (BSI-C, β = 9.189, t = 2.004, p = 0.048) among patients, but not among HC (β = 1.471, t = 0.825, p = 0.411), suggesting that gambling behavior has patient-specific predictive utility for suicidal symptoms.”

Page 19:

“Furthermore, linear regression showed that approach parameter can predict the current suicidal ideation score (β = 5.587, t = 2.890, p = 0.005) among patients, but not among HC (β = 0.874, t = 1.178, p = 0.241), suggesting that value-insensitive approach parameter has patient-specific predictive utility for suicidal symptoms.”

Page 21:

“Furthermore, linear regression showed that mood sensitivity to CR can predict the current suicidal ideation score (β = -28.706, t = -2.801, p = 0.006) among patients, but not among HC (β = -2.204, t = 0.528, p = 0.599), suggesting that mood sensitivity to CR has patient-specific predictive utility for suicidal symptoms.”

(3) The FDR correction for multiple comparisons mentioned briefly in lines 536-538 was not clear. Which analyses were included in the FDR correction? In particular, did the correlations between gambling rate and BSI-C/BSI-W survive such correction? Were there other correlations tested here (e.g., with the TAI score or ERQ-R and ERQ-S) that should be corrected for? Did the mediation model survive FDR correction? Was there a correction for other mediation models (e.g., with BSI-W as a predictor), or was this specific model hypothesized and pre-registered, and therefore no other models were considered? Did the differences in beta_gain across groups survive FDR when including comparisons of all other parameters across groups? Because the results were replicated in the online dataset, it is ok if they did not survive FDR in the patient dataset, but it is important to be clear about this in presenting the findings in the patient dataset.

Thank you for raising the important issue of multiple testing and for asking us to clarify exactly which tests were covered by the FDR procedure. In the clinical dataset we conducted a large number of inferential tests (χ², t-tests, ANOVAs, regressions) spanning: (i) group differences in demographic/clinical characteristics; (ii) sanity checks (e.g., anxiety/depression questionnaires); (iii) primary hypotheses (e.g., group differences in risky behavior); (iv) model-based analyses (parameter checks and between-group contrasts); and (v) control/sensitivity analyses. Post-hoc t-tests were performed only when the three-group ANOVA was significant. This yielded >150 p-values. FDR was applied using all these p-values. Please see our clarification below:

Supplementary Page 4:

“Supplementary Note 8: Clarification for FDR correction.

In the clinical dataset we conducted a large number of inferential tests (χ<sup2\</sup>, t-tests, ANOVAs, regressions) spanning: (i) group differences in demographic/clinical characteristics; (ii) sanity checks (e.g., anxiety/depression questionnaires); (iii) primary hypotheses (e.g., group differences in risky behavior); (iv) model-based analyses (parameter checks and between-group contrasts); and (v) control/sensitivity analyses. Post-hoc t-tests were performed only when the three-group ANOVA was significant. This yielded >150 p-values. FDR was applied using all these p-values.”

(4) There is a lack of explicit mention when replication analyses differ from the analyses in the patient sample. For instance, the mediation model is different in the two samples: in the patient sample, it is only tested in S+ and S- groups, but not in healthy controls, and the model relates a dimensional measure of suicidal symptoms to gambling in the task, whereas in the online sample, the model includes all participants (including those who are presumably equivalent to healthy controls) and the predictor is a binary measure of S+ versus S- rather than the response to item 9 in the BDI. Indeed, some results did not replicate at all and this needs to be emphasized more as the lack of replication can be interpreted not only as "the link between mood sensitivity to CR and gambling behavior may be specifically observable in suicidal patients" (lines 582-585) - it may also be that this link is not truly there, and without a replication it needs to be interpreted with caution.

Thank you for these important comments. This study focused on cognitive and affective computational mechanisms underlying increased risky behavior in STB. Accordingly, we compared patients with STB (S⁺) with patients without STB (S^-) and healthy controls (HC) to examine the effects of STB on risky behavior. Therefore, group comparison, instead of dimensional measure of suicidal symptoms by Beck Scale for Suicidal Ideation, can answer our research questions directly.

To enhance consistency between the clinical and replication datasets, we included all participants in each dataset when performing the mediation analysis. Given that S^- and HC did not differ in gambling behavior or the approach parameter in the clinical dataset, we merged these two groups. In the replication dataset, to mirror the S⁺ vs. S^- contrast used clinically, we categorized the general sample into S+ and S^- based on BDI item 9. The mediation results remained significant in both datasets (the clinical dataset: a×b = 0.321, 95% CI = [0.070, 0.549], p = 0.016; the replication dataset: a×b = 0.143, 95% CI = [0.016, 0.288], p = 0.031), suggesting that STB is associated with increased risk behavior via stronger approach motivation.

We also acknowledge the non-replication of the correlation between gambling behavior and mood sensitivity to certain rewards in the online sample. While this pattern might indicate that the link is specific to suicidal patients, it may also reflect sample-specific or unstable effects; thus, we now state this explicitly and interpret the finding with caution. Please see our revisions below:

Page 15:

“We next verified our results in an independent dataset, including the same task and BDI questionnaire in 747 general participants (500 females; age: 20.90±2.41) (46). One item in BDI involves the measurement of STB. In item 9 of BDI, participants chose one option that describes them best: Option 1, “I don't have any thoughts of killing myself.”; Option 2, “I have thoughts of killing myself, but I would not carry them out.”; Option 3, “I would like to kill myself.”; Option 4, “I would kill myself if I had the chance.”. In line with the current definition of S⁺/S^- in the clinical dataset, we identified S⁺ group as choosing Option 2, 3, or 4, while participants selecting Option 1 were categorized as S^- group.”

Page 19:

“Given significant correlations between group, approach parameter, and gambling rate for gain trials (ps < 0.017), we further conducted a mediation analysis with the assumption of the mediating effect of approach motivation of suicidality on the risk behavior. Given that we aimed to test the effect of STB, with S^- and HC as controls, and given that S^- and HC did not differ in gambling behavior or in the approach parameter, we merged these two groups for the mediation analysis. Results supported our hypothesis (a×b = 0.321, 95% CI = [0.070, 0.549], p = 0.016; Figure 2C), confirming that suicidal thoughts and behavior increase risk behavior through stronger approach motivation.”

Page 26:

“However, we did not observe any significant correlation between mood sensitivity to CR and gambling behavior (ps > 0.389), which suggests that the link between mood sensitivity to CR and gambling behavior may be specifically observable in suicidal patients. Alternatively, this non-replicated result may also reflect sample-specific or unstable effects, which needs to be interpreted with caution.”

(5) In interpreting their results, the authors use terms such as "motivation" (line 594) or "risk attitude" (line 606) that are not clear. In particular, how was risk attitude operationalized in this task? Is a bias for risky rewards not indicative of risk attitude? I ask because the claim is that "we did not observe a difference in risk attitude per se between STB and controls". However, it seems that participants with STB chose the risky option more often, so why is there no difference in risk attitude between the groups?

Thank you for pointing out the ambiguity. In our manuscript, “motivation” and “risk attitude” are defined at the computational level. Following prior work with this task Rutledge et al., (2015, 2016), we decompose observed gambling into (i) value-dependent valuation parameters that capture risk attitude (e.g., risk aversion and loss aversion, which scale the subjective value of outcomes), and (ii) value-insensitive, valence-dependent biases that capture approach/avoidance motivation. Accordingly, a higher gambling rate does not imply a change in risk attitude per se: it can arise from an increased value-insensitive approach bias even when risk-attitude parameters are comparable between groups—which is what we observe for S⁺ vs. controls. We have clarified this point in the computational modeling section.

Pages 12-13:

“Please note that a higher gambling rate does not imply a change in risk attitude per se: it can arise from an increased value-insensitive approach bias even when risk-attitude parameters are comparable between groups. Risk attitude is indeed conceptualized in economics as the curvature of the utility function (i.e., the subjective value) of the objective outcomes, with concave curves associated with risk aversion, and convex curves associated with risk seeking (54,56). By contrast, the approach or avoidance bias apply to all the value. A possible interpretation of the approach bias is that participant approach the option with the highest possible gain (the lottery) in the gain frame; the avoidance bias would then reflect a tendency to systematically avoid the highest potential losses (the lottery) in the loss frame.”

Reviewer #2 (Public review):

Summary:

This article addresses a very pertinent question: what are the computational mechanisms underlying risky behaviour in patients who have attempted suicide? In particular, it is impressive how the authors find a broad behavioural effect whose mechanisms they can then explain and refine through computational modeling. This work is important because, currently, beyond previous suicide attempts, there has been a lack of predictive measures. This study is the first step towards that: understanding the cognition on a group level. This is before being able to include it in future predictive studies (based on the cross-sectional data, this study by itself cannot assess the predictive validity of the measure).

Strengths:

(1) Large sample size.

(2) Replication of their own findings.

(3) Well-controlled task with measures of behaviour and mood + precise and well-validated computational modeling.

Weaknesses:

I can't really see any major weakness, but I have a few questions:

(1) I can see from the parameter recovery that the parameters are very well identified. Is it surprising that this is the case, given how many parameters there are for 90 trials? Could the authors show cross-correlations? I.e., make a correlation matrix with all real parameters and all fitted parameters to show that not only the diagonal (i.e., same data is the scatter plots in S3) are high, but that the off-diagonals are low.

Thank you for raising these thoughtful concerns. The current task consisted of 90 choices and 36 mood ratings. There were 5 choice parameters and 4 mood parameters. The apparently strong identifiability is not unexpected, as 90 choice trials and 36 mood ratings are comparable to those in prior computational modeling literature (Blain & Rutledge, 2022).

As suggested, we computed cross-correlations between all generating (“true”) and recovered (“fitted”) parameters. The resulting matrix showed high diagonal (choice winning model: rs > 0.91; mood winning model: rs > 0.90) and low off-diagonal (choice winning model: abs(rs) < 0.63; mood winning model: abs(rs) > 0.40) correlations, further supporting parameter recovery. Please see our clarifications below:

Supplementary Pages 2-3:

“Parameter recovery: Figure S3 shows good parameter recovery for both choice and mood winning model (choice: rs > 0.91, ps < 0.001; intraclass coefficients > 0.78; mood: rs > 0.90, ps < 0.001; intraclass coefficients > 0.86). Moreover, we computed cross-correlations between all generating (“true”) and recovered (“fitted”) parameters. The resulting matrix showed high diagonal (choice winning model: rs > 0.91; mood winning model: rs > 0.90) and low off-diagonal (choice winning model: abs(rs) < 0.63; mood winning model: abs(rs) > 0.40) correlations, further supporting parameter recovery.”

Page 10：

“The numbers of choice trials and mood ratings were comparable to those in prior computational modeling studies (34,35).”

(2) Could the authors clarify the result in Figure 2B of a correlation between gambling rate and suicidal ideation score, is that a different result than they had before with the group main effect? I.e., is your analysis like this: gambling rate ~ suicide ideation + group assignment? (or a partial correlation)? I'm asking because BSI-C is also different between the groups. [same comment for later analyses, e.g. on approach parameter].

Thank you for pointing out the lack of clarity. We performed group difference analysis and correlation of suicidal ideation analysis, separately. We first performed group difference analysis to test our hypothesis of STB effects. We then conducted correlational analysis to further specify our findings.

(3) The authors correlate the impact of certain rewards on mood with the % gambling variable. Could there not be a more direct analysis by including mood directly in the choice model?

Thank you for this insightful suggestion. As suggested, we tried to integrate mood into choice models by adding mood bias component(s) in line with previous literature (Vinckier et al., 2018). The first model (mcM1) assumes that mood biases choice, building on cM3 (the winning choice model). cmM2 further separated the mood bias parameter into two components according to participants’ choices.

However, model comparison using BIC supported cM3 (Table S6), that is, without consideration of mood in choice modeling. This can be due to the lack of block design in our experimental design unlike e.g., Vinckier et al., (2018) and Eldar & Niv, (2015). Please see our clarifications below:

Supplementary Pages 3-4:

“Supplementary Note 6: integration of mood into choice models

Although we modeled choice and mood separately to examine cognitive and affective mechanisms underlying increased risk behavior in adolescent suicidal patients, one interesting question was whether mood responses influence subsequent gambling choices and how to model them. First, we median-split mood responses (except the final rating) to compare gambling rate. Results showed a trend for less gambling rate in higher mood (t = -1.971, p = 0.050). However, there was no significant group difference (F = 0.680, p = 0.507). Second, with the assumption that mood biases choice, we constructed mcM1 based on cM3 (the winning choice model).

Based on our finding of the negative correlation between mood sensitivity to certain rewards and gambling rate in S⁺, we separated β_Mood parameter into β_Mood-CR and β_Mood-GR (cmM2).

Model comparison using BIC supported cM3 (Table S6), that is, without consideration of mood in choice modeling. The mood bias parameters in neither cM2 nor cM3 reached significance (ps > 0.091), which may be due to the absence of a blocked design in our experiment, unlike in Vinckier et al. (2018) and Eldar and Niv (2015).”

(4) In the large online sample, you split all participants into S+ and S-. I would have imagined that instead, you would do analyses that control for other clinical traits. Or, for example, you have in the S- group only participants who also have high depression scores, but low suicide items.

Thank you for this insightful suggestion. Following prior suicide-related literature (Tsypes et al., 2024), we controlled for depression by including them as covariates. Note that depression scores were derived from our established bifactor model (Wang et al., 2025), which decomposed depression from the anxiety. These results remained largely significant (ps ≤ 0.050), except a marginally significant effect of group on gambling behavior (p = 0.059). Despite a trend, this effect with covariates of depression-related questionnaires is strong in our clinical cohort (p = 0.024; Table S8). This suggests that the link between suicidality and risky behavior persists above and beyond general depressive symptoms.

Please see our clarifications below:

Page 26:

“After controlling for depression severity using our established bifactor model (see ref 60 for details), these results remained significant (ps ≤ 0.050), except a marginally significant effect of group on gambling behavior (p = 0.059). Despite a trend, this effect with covariates of depression-related questionnaires is strong in our clinical cohort (p = 0.024; Table S8). This suggests that the link between suicidality and risky behavior persists above and beyond general depressive symptoms.”

Reviewer #3 (Public review):

This manuscript investigates computational mechanisms underlying increased risk-taking behavior in adolescent patients with suicidal thoughts and behaviors. Using a well-established gambling task that incorporates momentary mood ratings and previously established computational modeling approaches, the authors identify particular aspects of choice behavior (which they term approach bias) and mood responsivity (to certain rewards) that differ as a function of suicidality. The authors replicate their findings on both clinical and large-scale non-clinical samples.

(1) The main problem, however, is that the results do not seem to support a specific conclusion with regard to suicidality. The S+ and S- groups differ substantially in the severity of symptoms, as can be seen by all symptom questionnaires and the baseline and mean mood, where S- is closer to HC than it is to S+. The main analyses control for illness duration and medication but not for symptom severity. The supplementary analysis in Figure S11 is insufficient as it mistakes the absence of evidence (i.e., p > 0.05) for evidence of absence. Therefore, the results do not adequately deconfound suicidality from general symptom severity.

Thank you for this important comment. Based on clinical interviews, we included patients with and without suicidality (S⁺ and S^- groups). However, in line with suicidal-related literature (e.g., Tsypes et al., 2024), two groups also differed substantially in the severity of symptoms (see Table 1). To address the request for evidence on specificity to suicidality beyond general symptom severity, we performed separate linear regressions to explain in gambling behaviour, value-insensitive approach parameter (β_gain), and mood sensitivity to certain rewards (β_CR) with group as a predictor (1 for S⁺ group and 0 for S^- group) and scores for anxiety and depression as covariates. Results remained significant after controlling anxiety and depression (ps < 0.027; Table S8). Given high correlations among anxiety and depression questionnaires (rs > 0.753, ps < 0.001), we performed Principal Components Analysis (PCA) on the clinical questionnaire to extract the orthogonal components, where each component explained 86.95%, 7.09%, 3.27%, and 2.68% variance, respectively. We then performed linear regressions using these components as covariates to control for anxiety and depression. Our main results remained significant (ps < 0.027; Table S9). We believe that these analyses provide evidence that the main effects on gambling and on mood were specific to suicide.

As pointed out, these “absence of evidence” cannot provide insights of “evidence of absence”. Although we median-split patients by the scores of general symptoms (e.g., depression and anxiety-related questionnaires) and verified no significant differences in these severities (Figure S11), we additionally conducted Bayesian statistics in gambling behavior, value-insensitive approach parameter, and mood sensitivity to certain rewards. BF₀₁ is a Bayes factor comparing the null model (M₀) to the alternative model (M₁), where M₀ assumes no group difference. BF₀₁ > 1 indicates that evidence favors M₀. As can be seen in Table S7, most results supported null hypothesis, suggesting that general symptoms of anxiety and depression overall did not influence our main results. Overall, we believe that these analyses provide compelling evidence for the specificity of the effect to suicide, above and beyond depression and anxiety.

Please see our revisions below:

Page 17:

“Within patients, this group effect on gambling rate remained significant after controlling for sex, illness duration, family history, diagnosis, and various medications use (ps < 0.05), as well as general symptoms (e.g., depression and anxiety; p = 0.024; also see Figure S11, Table S7 and Table S8). Given high correlations among anxiety and depression questionnaires (rs > 0.753, ps < 0.001), we performed Principal Components Analysis (PCA) to extract main components, where each component explained 86.95%, 7.09%, 3.27%, and 2.68% variance, respectively. To further control for anxiety and depression, linear regression using these components as covariates revealed that the group effect on gambling rate remained significant (p = 0.024; Table S9).”

Pages 18-19:

“Within patients, this group effect on the approach parameter remained significant after controlling for sex, illness duration, family history, diagnosis, and various medications use (ps < 0.05), as well as general symptoms (e.g., depression and anxiety; p = 0.027; also see Figure S11, Table S7 and Table S8). Linear regression using PCA components as covariates revealed that the group effect on approach parameter remained significant (p = 0.027; Table S9).”

Page 21:

“Within patients, this group effect on βCR remained significant after controlling for gambling rate, earnings, mood-related outcome effect, mood drift effect, sex, illness duration, family history, diagnosis, and various medications use (ps < 0.032), as well as general symptoms (e.g., depression and anxiety; p = 0.001; also see Figure S11, Table S7 and Table S8). Linear regression using PCA components as covariates revealed that the group effect on this mood parameter remained significant (p = 0.001; Table S9).”

(2) The second main issue is that the relationship between an increased approach bias and decreased mood response to CR is conceptually unclear. In this respect, it would be natural to test whether mood responses influence subsequent gambling choices. This could be done either within the model by having mood moderate the approach bias or outside the model using model-agnostic analyses.

Thank you for this important suggestion. As suggested, one interesting question was whether mood responses influence subsequent gambling choices and how to model them. First, we median-split mood responses (except the final rating) to compare gambling rate. Results showed a trend for less gambling rate in higher mood (t = -1.971, p = 0.050). However, there was no significant group difference (F = 0.680, p = 0.507). Second, with the assumption that mood biases choice, we constructed mcM1 based on cM3 (the winning choice model). Based on our finding of the negative correlation between mood sensitivity to certain rewards and gambling rate in S⁺, we separated β_Mood parameter into β_Mood-CR and β_Mood-GR (cmM2). Model comparison using BIC supported cM3 (Table S6), that is, without consideration of mood in choice modeling. This can be due to the lack of block design in our experimental design unlike e.g., Vinckier et al., (2018) and Eldar & Niv, (2015). Please see Supplementary Pages 3-4:

(3) Additionally, there is a conceptual inconsistency between the choice and mood findings that partly results from the analytic strategy. The approach bias is implemented in choice as a categorical value-independent effect, whereas the mood responses always scale linearly with the magnitude of outcomes. One way to make the models more conceptually related would be to include a categorical value-independent mood response to choosing to gamble/not to gamble.

We apologise for the unclear statement. The approach bias is implemented in choice as a continuous value-independent effect, ranging from -1 to 1.

It was true that the mood responses always scale with the magnitude of outcomes, since mood ratings were request after the outcomes. Therefore, mood parameters and the approach bias were both continuous.

We also attempted to integrate mood into choice modelling. See Response 2 for Reviewer 3 for details.

(4) The manuscript requires editing to improve clarity and precision. The use of terms such as "mood" and "approach motivation" is often inaccurate or not sufficiently specific. There are also many grammatical errors throughout the text.

Thank you for this important suggestion. We have now explained motivation and mood in the Introduction section and the computational modeling section. Please see our clarifications below:

Pages 3-4:

“A growing literature indeed shows that risky behavior can be far better explained after adding value-insensitive approach and avoidance components to prospect theory(18,19), that is by including a decision bias in favor of the highest gain (approach) and another decision bias against the lowest loss (avoidance), above and beyond options value difference. This class of models highlights the important role of value-insensitive motivational components in decision making in addition to risk attitude-driven valuation (e.g., loss/risk aversion)(20).”

Page 5:

“Although mood is thought to persist for hours, days, or even weeks(30-33), momentary mood, measured over the timescale in the laboratory setting, represents the accumulation of the impact of multiple events at the scale of minutes(30,32,34-38). Momentary mood external validity is demonstrated e.g., through its association with depression symptoms(37). Mood is different from emotions, which reflect immediate affective reactivity and is more transient (e.g., from surprise to fear)(31-33,39).”

We have corrected grammatical errors throughout the manuscript.

5) Claims of clinical relevance should be toned down, given that the findings are based on noisy parameter estimates whose clinical utility for the treatment of an individual patient is doubtful at best.

Thank you for this comment. We agree that we did not evaluate the noise in our estimate e.g., by assessing the test-retest reliability on the task parameters, which is outside the scope of the study, and it is indeed possible that parameter estimate is somehow noisy. Therefore, we tone down the clinical relevance of our results. Please see our revision below:

Page 32:

“Next, we did not evaluate the noise in our estimate e.g., by assessing the test-retest reliability on the task parameters and it is indeed possible that parameter estimate is somehow noisy.”

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Title: I believe "aberrant mood dynamics" is both too general and overstating the results of this study, which did not measure mood dynamics longitudinally. "Aberrant" is also overly pathologizing. I would suggest sticking more directly to the results, for instance, "Insensitivity of momentary mood to non-risky rewards in adolescent suicidal patients".

Thank you for this suggestion. We have now corrected it.

(2) Abstract: in line 61, "Our study uncovers the cognitive and affective mechanisms" suggests that these are the only ones, and you uncovered them. Of course, there could be more mechanisms contributing to risk behavior in STB, so I would suggest removing the word "the" or adding "one of the".

Thank you for this suggestion. We have now corrected it.

(3) One major weakness of this study is that suicidal thoughts and behaviors were not assessed via a clinical instrument such as the Columbia Suicide Severity Rating Scale - this should be mentioned upfront.

Thank you for this comment. According to medical records and information from family and friends by the researcher and psychiatrists, patients with suicidal thoughts and behaviors were categorized as suicidal group (S⁺), while patients without suicidal thoughts and behaviors were identified as control group (S^-). Note that medical records and information were recorded from clinical interviews where the psychiatrists were vigilant for signs of suicidal ideation and inquired about suicidal-related thoughts and behaviors from both the patients and their families. Therefore, the current group operation was possibly comparable to Columbia Suicide Severity Rating Scale.

(4) Table 1: female/male are sex, not gender (gender is man/woman/transgender/non-binary).

Thank you for this suggestion. We have now corrected it.

(5) Equation 1: It would be good to clarify what happens in gain-only or loss-only trials (the other value is then 0, but this can be clarified as it is not technically a loss or a gain).

Thank you for this suggestion. We have now corrected it. Please see below for our revision:

Page 12:

“Please note that V_gain is 0 in gain trials and V_loss is 0 in loss trials.”

(6) Figure 1E: The model prediction is not informative here. Given the linear regression model, there is no other option except that the mean prediction would overlap with the mean empirical measurement (unless the model was specified incorrectly). The same is true in Figure 2A.

Thank you for this suggestion. We have now removed plots for model prediction.

(7) Figure 1G: There was no analysis of the differences between groups in terms of earnings, given that the ANOVA was not significant. Still, if the claim is that risky behavior is sometimes suboptimal in this task, it would be good to show that there is a correlation between, say, symptoms of STB across groups and 1) risky behavior and 2) earnings.

Thank you for this insightful comment. In the patient cohort, risky behavior (gambling rate)—but not earnings—predicted the current suicidal ideation score (BSI-C, β = 9.189, t = 2.004, p = 0.048; earnings, β = 0.001, t = 0.582, p = 0.562). The lack of association for earnings is consistent with the task design, in which there is no stable optimal policy and payouts are only a coarse proxy for decision quality. Future work in learning paradigms, where optimality is well defined, may be better suited to test earnings-based links to STB. We have clarified this point below:

Page 32:

“Second, although we assumed that increased risky behavior in STB was suboptimal, the current task was not suited to test this, given the task design of random feedback for gambling option. Future work in learning paradigms, where optimality is well defined, may be better suited to test earnings-based links to STB.”

(8) Line 290: "beta_gain: -1-1" is unclear. I believe you meant beta_gain \in [-1,1].

Thank you for this suggestion. We have now corrected it to make it clear.

(9) The gain and loss biases are modeled as minimum and maximum probabilities for choosing the gamble. This is a legitimate choice for value-agnostic biases, but it is not the traditional choice (as far as I know). I wonder if the same results would hold with the more traditional formulation of the bias as an added constant to the utility of the gamble, i.e., p(gamble) = 1/(1+ exp(-mu(U_gamble + beta_gain - U_certain)). I believe in this case, you would also not have to specify different equations for positive or negative biases, or to limit the bias to the range of [-1,1] (indeed, the bias would be in reward-equivalent units).

Thank you for this suggestion. The winning choice model we used here was consistent with previous literature (Rutledge et al., 2015 & 2016), which decomposed the decision process into risk-attitude-driven valuation (e.g., loss and risk aversion) and value-insensitive motivational components. These approach/avoidance parameters are a decision bias in favor of the highest gain (approach) and another decision bias against the lowest loss (avoidance), above and beyond options value difference.

As suggested, we also compared the traditional bias choice model. Model comparison did not support this. Please see our revision below:

Supplementary Page 4:

“We also considered the traditional bias parameter (cM4), rather than approach/avoidance parameters. We limited the bias to the range of [-100, 100], which was in reward-equivalent units.

However, model comparison did not support cM4 (Table S6).”

(10) Also, for equations 5-8, it seems that 5-6 are identical to 7-8 except for the use of beta_gain versus beta_loss. You might want to consider simplifying by putting beta in the equations and specifying in the text that, depending on the trial type (loss or gain), the relevant beta is used.

Thank you for this suggestion. We have now simplified it. Please see response to Reviewer 2, point 3.

(11) It is not clear what equations are applied to mixed trials in cM3.

Sorry for the confusion. We have now clarified this point.

Page 12:

“Approach/avoidance parameters are not applied to in mixed trials.”

(12) Model comparison: the mood models are nested within each other (e.g., mM3 can be derived from mM1 by setting beta_EV = beta_RPE). In this case, model comparison can use the likelihood ratio test instead of BIC, which can be too conservative (and therefore does not support the extra beta parameter for RPE, different from previous results in the literature). I wonder if a likelihood ratio test would lead to results more in line with previous findings with this task?

Thanks for this suggestion. We agree that mM1 (CR+EV+RPE) and mM3 (CR+GR) are nested. However, our model space also included unnested models, such as mM5 (CR+GR_better+GR_worse). Therefore, it was not reasonable in our model space to use likelihood ratio tests.

(13) Line 346: The replication sample is described as "healthy participants," however, their health (or mental health) status was not assessed, and they may as well have mental health concerns. I would suggest calling this a general sample or an undifferentiated sample - but not a healthy sample.

Sorry for the confusion. We have now corrected this phrase.

(14) Line 363: "in addition to the replication of previous findings in the validation dataset" is unclear. Are those tests not two-tailed?

Sorry for the unclear statement. In the replication analyses, we used one-tailed t-tests because the direction of the effect was revealed on the clinical dataset. Please see our clarification below:

Page 15:

“For the replication of previous findings in the validation dataset, we used one-tailed tests in line with our clinically motivated directional hypothesis.”

(15) Line 372: "validating our group manipulation" - the presented work does not have a manipulation. Maybe you meant "validating our grouping of participants"?

Thank you for this suggestion. We have now corrected it to make it clear.

(16) Figure 2B: It is not clear how the data were binned for illustration purposes only, and why this binning is necessary (I have not seen it in other papers) - presenting the data from each subject and the correlation line with error margins (as is done here) should be sufficient.

Thank you for flagging this. For illustration only, we binned the data proportional to group sizes: in the patient sample (S^- n = 25; S⁺ n = 58; ≈1:2), we displayed 3 bins for S^- and 6 bins for S⁺. We agree that binning is not necessary; all statistics were computed on raw, unbinned data. The binned panel was included solely for visualization, consistent with our prior work (Blain et al., 2023).

(17) Table 2: delta BIC should be presented per subject (that is, divided by the number of subjects in each group), as the groups are of different sizes, so as presented now, the columns are not comparable across groups.

Thank you for the helpful suggestion. Our goal in Table 2 is not to compare ΔBIC magnitudes across groups, but to identify the winning model within each group. The ΔBICs are aggregated at the group level solely to rank models for that group. Dividing by the number of participants would rescale each group’s column by a constant and would therefore not affect the within-group ranking or the conclusion that cM3 is the best model in all groups. For this reason, we retain the current presentation and interpret each column within group rather than across groups.

(18) Line 640 - the effect of expectations and prediction errors on mood was not only shown in healthy people, but also in people with depression (Rutledge et al., 2007, https://pubmed.ncbi.nlm.nih.gov/28678984/)

Thank you for this comment. Indeed, Rutledge et al., (2017) showed evidence for CR+EV+RPE mood model in adult people with depression. However, our study recruited adolescents with depression or anxiety, given that adolescent period might provide a developmental window for opportunities for early intervention of suicidality. Therefore, it is also possible that the current winning model was specific to adolescents. Please see our clarifications below:

Page 28:

“It is also possible that the current winning model was specific to adolescents. Given that Rutledge et al., (2017) supported the “CR-EV-RPE model” in adults with depression, our study with adolescent populations may suggest a developmental change for mood sensitivities.”

(19) Supplemental material: Is the R2 section about R-squared? Perhaps you can use superscript on the 2 to make that clearer? For Figure S2, how was model recovery determined? Should I interpret the confusion matrix as suggesting that the winning model for each and every simulated subject was the generating model, or was the winning model determined for the whole simulated population in each of the 100 simulations? Traditionally, confusion matrices use the former measure, but the results of 100% recoverability make me suspect the latter was used here. In Figure S3, should we not be looking at simulated parameters and recovered parameters? What are "real parameters" here?

Thank you for these important comments. We now consistently denote the coefficient of determination as R² (with a superscript 2) throughout the manuscript and Supplementary Materials.

For the model recovery analysis in Figure S2, we have clarified that the confusion matrix is computed at the population level. Specifically, for each of the 100 simulations we generated a full dataset under each candidate model, fit all models to that dataset, and selected the winning model based on group-level model evidence (BIC). Each cell in the confusion matrix therefore reflects the proportion of simulations in which model j was selected as the best-fitting model when the data were generated by model i. This operation was reasonable because the decision of the winning model is made on the population-level dataset rather than on individual subjects.

In Figure S3, the term “real parameters” referred to the parameters used to generate the simulated data. To avoid confusion, we now relabel these as “simulated (generating) parameters” and explicitly describe the figure as showing the relationship between simulated (generating) parameters and recovered parameters. Please see our revisions below:

Supplementary Pages 2-3:

“Model recovery: We generated 100 simulated datasets for each model (3 choice models and 8 mood models) using the fitted parameters of each model as the ground truth. Each dataset contained 201 trials and included 3 (or 8) sets of simulated data corresponding to the respective models. For each simulated dataset, we then fit all models and determined the winning model at the population level based on group-level BIC, yielding a confusion matrix in which each entry represents the proportion of simulations in which model j was selected as the best-fitting model when the data were generated by model i. As shown in Figure S2, all models are highly identifiable, indicating excellent recovery performance for both the choice and mood models.”

“Parameter recovery: Figure S3 shows good parameter recovery for both choice and mood winning model (choice: rs > 0.91, ps < 0.001; intraclass coefficients > 0.78; mood: rs > 0.90, ps < 0.001; intraclass coefficients > 0.86). Moreover, we computed cross-correlations between all generating (“generating”) and recovered (“fitted”) parameters. The resulting matrix showed high diagonal (choice winning model: rs > 0.91; mood winning model: rs > 0.90) and low off-diagonal (choice winning model: abs(rs) < 0.63; mood winning model: abs(rs) > 0.40) correlations, further supporting parameter recovery.”

Typos:

(1) Line 90: original → originate

(2) Line 596-598 - the same phrase is repeated twice.

(3) Line 616: on the other word → hand.

Sorry for the mistakes. We have now corrected them throughout the manuscript.

Reviewer #2 (Recommendations for the authors):

For people unfamiliar with interpersonal theory or motivational-volitional model, or three-step theory (lines 105-106), could you briefly explain the key idea of mood and suicide before going to the decision-making tasks? And from this, maybe motivate the predictions in your task? In particular, in the abstract and introduction, the phrasing could be a bit more concise and simpler. In the abstract, sentences were sometimes quite long. In the introduction, some paragraphs are somewhat repetitive. In the discussion, there were some typos.

Thank you for these suggestions. We have now explained the key idea of mood and suicide before going to the decision-making tasks in the introduction, which can be seen below:

Pages 4-5:

“Contemporary theories of suicide converge on the idea that STB is initially caused by low mood experience. The interpersonal theory of suicide proposes that suicidal desire arises when people simultaneously feel socially disconnected (“thwarted belongingness”) and like a burden on others (“perceived burdensomeness”), experiences that are tightly linked to chronically low mood(25). The motivational–volitional model(26) and the three-step theory(27,28) similarly emphasize that when negative mood and feelings of defeat or entrapment are experienced as inescapable, they can give rise to suicidal ideation, and that the progression from ideation to suicide attempts depends on additional factors such as reduced fear of death, increased pain tolerance, and a tendency to act impulsively under intense affect. Some official organizations, e.g., National Institute of Mental Health, have also listed mood problems as warning signals(8). Interestingly, within the framework of decision making under uncertainty, gambling on lotteries with a revealed outcome has been found to induce high mood variance(29), providing an opportunity to assess the relationship between deficient mood and increased gambling decisions in STB.”

We have also refined the wording and corrected typos throughout the manuscript.

Reviewer #3 (Recommendations for the authors):

(1) Since many readers might only read the abstract, it is important that it is both informative and accurate. I have two suggestions in this respect. First, for the abstract to be more informative, it may be helpful to indicate already there that these are value-insensitive approach-avoidance parameters, in the sense that they favor/disfavor the gamble regardless of the potential outcomes' magnitude or probability. This issue is also present throughout the text, where the phrases "approach and avoidance motivation" are referred to as if they have established and precise computational definitions. In my view, these terms could just as easily be interpreted as parameters that multiply the value of potential gains or losses, which is not what the authors mean. It would be helpful to clarify this terminology.

Thank you for these suggestions. In line with previous literature (Rutledge et al., 2015 & 2016), approach and avoidance motivation are indeed defined at the computational level, referring to a decision bias in favor of the highest gain (approach) and another decision bias against the lowest loss (avoidance), above and beyond options value difference. We have cited these papers in the manuscript. We also make it clear to further clarify approach and avoidance parameters in the abstract and introduction. Please see our revisions below:

Page 2 (Abstract):

“Using a prospect theory model enhanced with value-insensitive approach-avoidance parameters revealed that this rise in risky behavior resulted only from a heightened approach parameter in S⁺.Altogether, model-based choice data analysis indicated dysfunction in the approach system in S⁺, leading to greater propensity for gambling in the gain domain regardless of the lottery expected value.”

Page 3 (Introduction):

“A growing literature indeed shows that risky behavior can be far better explained after adding value-insensitive approach and avoidance components to prospect theory(18,19), that is by including a decision bias in favor of the highest gain (approach) and another decision bias against the lowest loss (avoidance), above and beyond options value difference. This class of models highlights the important role of value-insensitive motivational components in decision making in addition to risk attitude-driven valuation (e.g., loss/risk aversion)(20).”

(2) The statement "our study uncovers the cognitive and affective mechanisms contributing to increased risk behavior in STB" is overstating the findings, as the study may have uncovered some contributing mechanisms, but likely not all of them. Removing the word "the" would fix this issue.

Thank you for this suggestion. We have now corrected it.

(3) Since mood is typically defined as lasting hours, it's inappropriate to refer to ratings that only reflect the last few trials as self-reports of mood. To be sure, I view the distinction between emotions and moods as quantitative, not qualitative, so I do not think there is a problem studying the former to understand the latter, but to avoid confusion, the terminology should follow common usage.

Thank you for this suggestion. We follow previous work and operational definitions regarding mood (Rutledge et al., 2014, Eldar & Niv, 2015, Vinckier et al., 2018). Emotion is usually a very brief response to a specific stimulus (Emanuel & Eldar, 2023), e.g., leading to rapid changes like surprise then fear. In contrast, mood is defined as a diffuse state that is not specific to one stimulus. Here, we operationally and computationally define mood as an affective state reflecting the recent history of safe and gamble outcomes. We now clarify that point in the main text. Please see our revision below:

Page 5:

“Although mood is thought to persist for hours, days, or even weeks(30-33), momentary mood, measured over the timescale in the laboratory setting, represents the accumulation of the impact of multiple events at the scale of minutes(30,32,34-38). Momentary mood external validity is demonstrated e.g., through its association with depression symptoms(37). Mood is different from emotions, which reflect immediate affective reactivity and is more transient (e.g. from surprise to fear)(31-33,39).”

(4) Line 78: The phrases "increase in risk attitude", "decrease in loss attitude", and "decrease in value-independent choice biases" are unclear to me in terms of their directionality. An attitude might be avoidant or embracing. If it is the former then increasing it would decrease risk-taking.

Thank you for pointing out the ambiguity. We have now corrected them throughout the manuscript. Please see our revision below:

Page 4:

“We therefore hypothesized that heightened approach motivation, or weakened avoidance motivation, would account for increased risk behavior in STB.”

(5) Line 125: I was not sure why one would expect the mood response to gamble-related quantities (EV and RPE) to be lower in STB and not higher.

Sorry for the typo. We hypothesized that mood would respond more strongly to gambling-related quantities—expected value (EV) and reward prediction error (RPE)—in adolescents with STB than in controls, given prior evidence that STB is associated with greater risk-taking.

(6) The text could use proofreading, as there are many typos. These are from the first 100 lines alone:

a) Abstract: regardless the lotteries -> regardless of the lotteries'.

b) Line 78: it remains whether.

c) Line 80: can each -> each can.

d) Line 90: may original from.

Sorry for the mistakes. We have now corrected them throughout the manuscript.

(7) The rationale for focusing on the S+ group for mood model comparison is incorrect. The purpose is to identify parameters that vary as a function of suicidality, and for that, the S- group is just as important.

Thank you for this comment. We agree that the S^- group is as important as the S⁺ group. A direct comparison was complicated because the winning mood models differed (S⁺: mM3; S^-: mM5; Table 3). To ensure comparability, we checked results from both model specifications (mM3 and mM5). The conclusions were convergent: mood sensitivity to certain rewards (CR) was lower in S⁺ than in S^- (see Fig. 3 for mM3 and Fig. S8 for mM5).

(8) There appears to be a contradiction between the inclusion criteria, which include having experienced suicidal thoughts and behaviors, and the definition of the S- group as not having suicidality.

Thank you for pointing out this mistake. The corrected version of inclusion criteria can be seen on Page 7:

“Patients were included if they met the following criteria: 1) both the researcher and psychiatrists agreed on their group classification; 2) they had a current diagnosis of major depressive disorder (MDD; unipolar depression), generalized anxiety disorder (GAD), or bipolar disorder with depressive episodes (BD), confirmed by two experienced psychiatrists using the Structured Clinical Interview for DSM-IV-TR-Patient Edition (SCID-P, 2/2001 revision; see Supplementary Note 1 for details); 3) they were between 10 and 19 years of age; 4) they had no organic brain disorders, intellectual disability, or head trauma; 5) they had no history of substance abuse; 6) they had no experience of electroconvulsive therapy.”

(9) It would be helpful to specify whether mood modeling was based on objective or subjective values, and why.

Thank you for this helpful suggestion. We have now clarified whether mood modeling was based on objective or subjective values, and why. Specifically, we constructed two model families: one in which mood was driven by objective monetary outcomes (objective values) and one in which mood was driven by subjective values derived from each participant’s fitted choice model (subjective values). We then used the VBA_groupBMC function in the VBA toolbox to perform family-wise model comparison, with 8 candidate mood models within each family. Consistent with previous literature, the objective-value family provided a clearly superior fit to the data (exceedance probability, EP = 1.000). Based on this result and for parsimony, we report and interpret the mood modeling results from the objective-value family in the main text. We have clarified this point below:

Supplement Pages 4-5:

“Supplementary Note 9: Mood model comparison using subjective values.

To identify whether mood modeling was based on objective or subjective values, we constructed two model families: one in which mood was driven by objective monetary outcomes (objective values) and one in which mood was driven by subjective values derived from each participant’s fitted choice model (subjective values). We then used the VBA_groupBMC function in the VBA toolbox (Daunizeau et al., 2014) to perform family-wise model comparison, with 8 candidate mood models within each family. Consistent with previous literature, the objective-value family provided a clearly superior fit to the data (exceedance probability, EP = 1.000).”

Author Response:

The following is the authors’ response to the previous reviews

Public Review:

We thank the editor and reviewers for their thoughtful and constructive feedback, which has enabled us to greatly strengthen the manuscript. We apologize for the delay in resubmitting this as we were dealing with a large turnover in the lab due to trainee graduations which has We have carefully revised the text, figures, and supplementary materials in response to these comments. Below, we summarize the key revisions made followed by a point-by-point response to the reviewers’ critiques.

(1) Performed CUTS analyses in human neuronal system: In the revised manuscript, we included new data demonstrating that the CUTS system can be applied to additional cellular models, specifically neuronal cells (Figure 5, Figure S4). To address whether CUTS functions effectively in neuronal contexts, we generated stable CUTS-expressing lines in differentiated BE(2)-C and ReN VM–derived differentiated neurons (Figure 5A-D, Figure S4 A-C). To ensure this was neuronal expression, we developed a new Tet-On3G system construct where the Tet-On3G transactivating protein is driven by the SYN1 promoter to ensure neuron-specific inducible expression for these experiments.

(2) Define the relationship between CUTS and endogenous/physiological cryptic exons inclusion: To evaluate how well the CUTS system reflects physiological cryptic exon regulation, we performed RT-PCR analysis of several cryptic exons previously reported by us and evaluated CUTS activation at the RNA level in parallel (Figure S2E) . CUTS is sensitive to low-mild reductions in TDP-43 levels, whereas the tested endogenous cryptic exons exhibit variable responses to TDP-43 knockdown.

(3) Defining stress-induced TDP-43 loss of function: We included new data demonstrating that the CUTS system can detect TDP-43 loss of function induced by acute sodium arsenite (NaAsO₂) treatment in HEK cells (Figure 3D–I). We have also tested additional stressor as part of a separate ongoing study where this work will be expanded upon (Xie et al., 2025). We selected this paradigm since TDP-43 loss of function in response to acute NaAsO₂ treatment is also supported by work from other labs(Huang et al., 2024).

(4) Implications of using a TDP-43 Loss-of-Function sensor for therapeutic applications: In the revised manuscript, we clarify that CUTS-TDP43 is auto-regulated and we highlight two potential therapeutic applications: i) TDP-43 Knockdown-and-replacement: CUTS-TDP43 provides a strategy for simultaneous depletion of pathological TDP-43 species while enabling autoregulated re-expression of wild-type TDP-43. This design mitigates the risk of supraphysiologic overexpression, a known liability in conventional replacement approaches, by restoring TDP-43 within a self-limiting regulatory network that maintains homeostatic control. ii) Aggregation-independent correction: Because CUTS is autoregulatory, it can be repurposed to regulate alternative downstream effectors, including splicing modifiers or TDP-43 functional interactors, without expressing TDP-43 itself. This approach provides a potential aggregation-independent strategy to compensate for TDP-43 loss-of-function (LOF) by restoring downstream splicing. We are evaluating this work in a follow up study (Xie et al., 2025). In these ongoing studies, we show that CUTS-regulated expression of splicing proteins in response to TDP-43 loss restored subsets of cryptic exon events (24/28 events evaluated). These findings suggest CUTS as a versatile tool for both autoregulated TDP-43 replacement and trans-regulatory therapeutic correction. We expanded on this concept in the discussion section of this revised manuscript. We also note that autoregulatory TDP-43 biosensor strategies have been proposed in related systems, including TDP-Reg, underscoring broader interest in self-regulated TDP-43 systems (Wilkins et al., 2024).

(5) Clarified mechanism of TDP-43 5FL causing strong loss of function: The TDP-43 5FL exhibits reduced RNA binding capacity, and we previously showed that the lack of RNA binding promotes aberrant homotypic phase separation of TDP-43 (Mann et al., 2019). Expression of RNA-deficient TDP-43 variant forms nuclear “anisomes” (Yu et al., 2021), which evidence suggests sequesters endogenous TDP-43 protein into insoluble structures. We expanded on this in our results section in this revised manuscript.

(6) Improved figure clarity and data presentation: To enhance clarity and organization, we maintained the main structure of the manuscript while reorganizing figures and improved data visualization. Some examples include:

Figure 1: We revised the schematic layout for greater clarity and simplicity. The figure now focuses more specifically on the CUTS data, with additional data on the UNC13A-TS and CFTR-TS moved to Figure S1. To improve readability, titles were added to all schematic panels. Visual consistency was also improved by refining the color labelling for each sensor in Figures 1C and 1D and adjusting the corresponding bar graphs accordingly.

Figure 2: We reorganized the figure to clearly distinguish between protein and mRNA analyses for greater clarity. In the revised layout, western blot quantifications of TDP-43 and CUTS (GFP) signals are shown in Figures 2D and 2E, respectively, while the corresponding qPCR analyses are presented in Figures 2H and 2I. Minor edits include removing the percentage knockdown and fold-change annotations from the graphs and incorporating these values into a mini-table in Figure S2E.

The original Figure 2D and 2G were reincorportated as reference panels in Figure S2A–B, while new graphs showing CUTS protein-level changes as a function of TDP-43 knockdown were added (Figure S2C–D). We also incorporated new data showing the behavior of endogenous cryptic exons under low siTDP-43 treatment (Figure S2E).

Figure 3: We added new data demonstrating that the application of the CUTS system in detecting TDP-43 loss of function induced by stress conditions. Specifically, we show that sodium arsenite (NaAsO₂) treatment leads to TDP-43 functional impairment detectable by CUTS and supported with endogenous cryptic exon via RT-PCR (Figure 3D-I).

Figure 5 and Figure S4: We introduced a new figure that demonstrates the effective application of the CUTS system in differentiated neuronal systems, thereby extending its usability to disease-relevant cell types.

Figures 2SA and 4B were edited to include the corresponding labels on the sides of each image for clarity. Sup Figure 2A was moved to Sup Figure 3A, while Figure 4B remains in its original configuration.

We thank the reviewers again for their insightful critiques and helpful suggestions, which have enabled us to substantially improve the manuscript. Please find our detailed response to each review below:

Reviewer #1 (Public review):

Summary:

The authors create an elegant sensor for TDP -43 loss of function based on cryptic splicing of CFTR and UNC13A. The usefulness of this sensor primarily lies in its use in eventual high throughput screening and eventual in vivo models. The TDP-43 loss of function sensor was also used to express TDP-43 upon reduction of its levels.

Strengths:

The validation is convincing, the sensor was tested in models of TDP-43 loss of function, knockdown and models of TDP-43 mislocalization and aggregation. The sensor is susceptible to a minimal decrease of TDP-43 and can be used at the protein level unlike most of the tests currently employed,

Weaknesses:

Although the LOF sensor described in this study may be a primary readout for high-throughput screens, ALS/TDP-43 models typically employ primary readouts such as protein aggregation or mislocalization. The information in the two following points would assist users in making informed choices.

(1) Testing the sensor in other cell lines

We thank the reviewer for raising this important point. In agreement with this suggestion, we generated ReN VM cell lines and used a neuroblastoma cell line model (BE(2)-C) expressing the TetOn3G CUTS system under a human synapsin I (hSYN1) promoter. In this construct the transactivator protein is under the control of a neuronal specific hSYN1 promoter whereas the classical TetOn3G system uses a CMV-like promoter. Several studies have reported reduced activity or silencing of CMV and PGK-driven transgenes in neurons. Therefore, we for our neuronal experiments, we removed this promoter to generate a new version of a doxycycline-inducible CUTS system in which Tet-On 3G transactivator is now driven by the hSYN1 promoter which will express CUTS in response to doxycycline treatment. In this improved construct, we also replaced mCherry with mScarlet to enhance the fluorescent signal.

To test this neuronal-adapted system, we established stable CUTS expression in undifferentiated BE(2)-C cells, a subclone of the SK-N-BE(2) neuroblastoma line that has been used to study TDP-43–dependent splicing function(Brown et al., 2022). This model can be differentiated into neuron-like cells within 10 days, as shown in Supplementary Figure 4A. Using this model, we confirmed that TDP-43 knockdown leads to robust activation of the CUTS system (Figure 5B-E). We additionally tested this in in a stable polyclonal ReN VM cells following differentiation into cortical-like neurons (Figure 5D, Figure S4B-C).

(2) Establishing a correlation between the sensor's readout and the loss of function (LOF) in the physiological genes would be useful given that the LOF sensor is a hybrid structure and doesn't represent any physiological gene. It would be beneficial to determine if a minor decrease (e.g., 2%) in TDP-43 levels is physiologically significant for a subset of exons whose splicing is controlled by TDP43.

We agree with the reviewer that correlating the sensor’s readout with physiological TDP-43 splicing targets is essential to validate its biological relevance. To this end, we complemented our sensor expression profile with endogenous cryptic exons (CEs) sensitive to TDP-43 depletion. We tested a panel of five physiological cryptic exons regulated by TDP-43 (LRP8, EPB41L4A, ARHGAP32, HDGFL2, and ACBD3). To address the reviewer’s concerned, we performed RT-PCR on samples from the low-dose siTDP-43 experiment shown in Figure S2E.

The endogenous CEs used in the panel were selected based on our own and others’ preliminary observations. Among these, HDGFL2 showed a particularly robust increase in cryptic exon inclusion at very low siTDP-43 concentrations (38 pM), while untreated samples showed almost no CE inclusion. This finding strongly supports a direct mechanism linking mild TDP-43 reduction to loss of physiological splicing control.

(3) Considering that most TDP-LOF pathologically occurs due to aggregation and or mislocalization, and in most cases the endogenous TDP-43 gene is functional but the protein becomes non-functional, the use of the loss of function sensor as a switch to produce TDP-43 and its eventual use as gene therapy would have to contend with the fact that the protein produced may also become nonfunctional. This would eventually be easy to test in one of the aggregation modes that were used to test the sensor.. However, as the authors suggest, this is a very interesting system to deliver other genetic modifiers of TDP-43 proteinopathy in a regulated fashion and timely fashion.

We thank the reviewer for this thoughtful point and agree that in the disease-relevant context where endogenous TDP-43 is intact but TDP-43 function is lost due to mislocalization and/or aggregation, a re-supply of TDP-43 risks sequestration and loss of activity. In our manuscript, the CUTS-TDP43 module was presented as a control circuit proof-of-concept rather than a stand-alone approach: it demonstrates that CUTS can (i) sense LOF with high dynamic range and proportionality, and (ii) drive a payload under negative feedback such that total TDP-43 remains near baseline while partially rescuing a splicing readout (CFTR minigene) under knockdown conditions.

Importantly, we evaluated CUTS in aggregation/mislocalization-prone contexts: ΔNLS, 5FL, and ΔNLS+5FL variants trigger CUTS activation (ref), allowing us to quantify LOF arising from these aggregation modes. This confirms that CUTS can operate precisely in the very settings where sequestration is likely to occur.

To directly address the reviewer’s suggestion, in the revision we (i) clarify in the Discussion that CUTS-TDP43 is a circuit demonstration and not our proposed monotherapy in aggregation-dominant disease; and (ii) expand our therapeutic framing into two approaches:

Knockdown-and-replacement: concurrently deplete aggregation-prone/endogenous pathologic TDP-43 species (i.e., mutant TDP-43) while using CUTS to re-deliver wild-type TDP-43 under autoregulation. Aggregation-independent correction: use of CUTS to deliver modifiers that bypass TDP-43 sequestration (e.g., downstream effectors or splicing correctors that restore LOF consequences without expressing TDP-43 itself).

(4) I don't think the quantity of siRNA is directly proportional to the degree of TDP-43 knockdown/extent of TDP-43 loss. Therefore, to enhance the utility of the dose-response curves, I'd suggest using TDP-43 levels as the variable on the x-axis, rather than the amount of siRNA administered or even just adding a plot alongside the current plots would enable readers to quickly evaluate LOF response levels concerning the protein. While I understand that the sensitivity of Western blots for quantification might be why the authors have not created the graphs in this manner, having this information would be useful.

We appreciate the reviewer’s insightful comment. As noted, in the original version of the graph, we incorporated the percentage of TDP-43 knockdown corresponding to each siTDP-43 concentration (indicated in red text). However, we agree that this format was not easy to interpret, given the amount of information presented. To address this, we generated two new plots in which the x-axis represents TDP-43 levels (percentage of remaining protein or mRNA), and the y-axis shows the fold change in CUTS signal measured by (i) TDP-43 protein pixel intensity and (ii) TDP-43 mRNA levels, respectively. These new plots are now included as Supplementary Figures 2C–D, which allow a clearer visualization of CUTS readout in relation to actual TDP-43 levels rather than siRNA dose. As the reviewer anticipated, the reason we did not originally present the data in this format was that at low siTDP-43 concentrations, the fold change is minimal and more difficult to quantify by Western blot. Nevertheless, we have now incorporated the revised plots to strengthen the interpretation of the dose–response relationship. Additionally, we experience batch effects across siRNA lots. We believe this revised format should enhance the clarity of the result.

(5) p3 line 74: one of the reasons cited as a pitfall of using the endogenous cryptic exons exhibit variable responses to TDP-43 loss and may be cell type-specific. has the sensor been used in different cell lines?

We tested the CUTS system in differentiated neuronal models using two differentiated neuronal cell types, BE(2)C and ReN VM cells. The results are presented in Figure 5 and Figure S4 of the revised manuscript.

(6) The order of the text describing 1A and 1B is confusing. The text starts describing the TS cassettes referring to 1A using the CUTS cassettes which haven't been introduced yet as an example. I'd suggest reorganising this section. The graph, always in 1A showing readout proportional to GFP should be taken out or highlighted in the figure legend that it is theoretical.

We agree with the reviewer’s point. In the original schematic (Figure 1A), we included the CUTS system as an example to introduce the TS cassette design, since it contains the three possible sensor configurations. However, we recognize that this could be confusing. Therefore, we have removed the CUTS cassette from Figure 1A, along with the theoretical graph showing GFP readout proportional to the degree of TDP-43 LOF. In agreement with this change, we also restructured Figure 1. As the focus is the CUTS system, we have moved the Western blot and quantification of UNC13A-TS and CFTR-TS to Supplementary Figure 1.

Reviewer #2 (Public review):

Summary:

The authors goal is to develop a more accurate system that reports TDP-43 activity as a splicing regulator. Prior to this, most methods employed western blotting or QPCR-based assays to determine whether targets of TDP-43 were up or down-regulated. The problem with that is the sensitivity. This approach uses an ectopic delivered construct containing splicing elements from CFTR and UNC13A (two known splicing targets) fused to a GFP reporter. Not only does it report TDP-43 function well, but it operates at extremely sensitive TDP-43 levels, requiring only picomolar TDP-43 knockdown for detection. This reporter should supersede the use of current TDP-43 activity assays, it's cost-effective, rapid and reliable.

Strengths:

In general, the experiments are convincing and well designed. The rigor, number of samples and statistics, and gradient of TDP-43 knockdown were all viewed as strengths. In addition, the use of multiple assays to confirm the splicing changes were viewed as complimentary (ie PCR and GFPfluorescence) adding additional rigor. The final major strength I'll add is the very clever approach to tether TDP-43 to the loss of function cassette such that when TDP-43 is inactive it would autoregulate and induce wild-type TDP-43. This has many implications for the use of other genes, not just TDP-43, but also other protective factors that may need to be re-established upon TDP-43 loss of function.

Weaknesses:

(1) Admittedly, one needs to initially characterize the sensor and the use of cell lines is an obvious advantage, but it begs the question of whether this will work in neurons. Additional future experiments in primary neurons will be needed.

We thank the reviewer for highlighting the importance of validating the sensor in neuronal models, given the central role of TDP-43 dysfunction in ALS/FTD and related neurodegenerative disorders. While initial characterization in established cell lines provides experimental control and scalability, we agree that demonstrating functionality in neuronal systems is essential. To address this, we adapted the CUTS platform for neuronal application by incorporating the human synapsin-1 (hSYN1) promoter into the Tet-On 3G system to enable inducible, neuronal specific expression. We validated this configuration in differentiated BE(2)-C cells (Figures 5A-C, S4A-C), where CUTS retained robust responsiveness to TDP-43 perturbation. In parallel, we generated stable CUTS-expressing ReN VM neural progenitor cells and differentiated them for three weeks prior to functional assessment (Figures 5A-C, S4A-C). In both neuronal models, CUTS was functional and responsive to TDP-43 siRNA. We are currently optimizing promoter selection and expression paradigms for fully differentiated iPSC-derived neuronal models and will be the subject of future studies.

(2) The bulk analysis of GFP-positive cells is a bit crude. As mentioned in the manuscript, flow sorting would be an easy and obvious approach to get more accurate homogenous data. This is especially relevant since the GFP signal is quite heterogeneous in the image panels, for example, Figure 1C, meaning the siRNA is not fully penetrant. Therefore, stating that 1% TDP-43 knockdown achieves the desired sensor regulation might be misleading. Flow sorting would provide a much more accurate quantification of how subtle changes in TDP-43 protein levels track with GFP fluorescence.

We thank the reviewer for this thoughtful suggestion. We agree that flow cytometry and sorting of GFP-positive populations would provide a higher-resolution, single-cell–level relationship between TDP-43 abundance and sensor output. Such an approach would reduce heterogeneity arising from incomplete siRNA penetrance and allow more precise quantification of how incremental changes in TDP-43 protein levels track with GFP fluorescence. In the present study, our goal was to establish proof-of-principle functionality of the CUTS circuit and to demonstrate that graded TDP-43 depletion produces a proportional sensor response at the population level. While GFP signal heterogeneity is visible in imaging panels, we hypothesize that this variability likely reflects known differences in siRNA uptake and transfection efficiency rather than instability of the circuit itself. Importantly, bulk measurements consistently demonstrated dose-dependent sensor regulation across independent experiments, supporting the robustness of the system despite cellular heterogeneity. Furthermore, we were able to quantify CUTS activation in HeLa TARDBP^-/- cells. We also note that CUTS was developed as a practical tool for rapid assessment of TDP-43 LOF in standard laboratory settings. Although flow cytometry increases resolution, the ability to detect functional perturbation using bulk fluorescence measurements supports the utility of the system for routine and high-throughput applications.

We agree that flow cytometry would provide a more refined analysis of the dynamic range and sensitivity of CUTS, particularly for defining thresholds such as minimal TDP-43 knockdown required for measurable activation. We plan to include this work in future studies. Specifically, we have implemented FACs sorting of CUTS-expressing cells in a parallel study in which we are conducting a CRISPR knockout screen to identify modifiers of TDP-43 splicing function. For this, we incorporate TDP-43 knockdown followed by FACs to stratify cells based on CUTS activation. This strategy enables direct evaluation of the relationship between the extent of TDP-43 LOF and CUTS sensor activation. These analyses are ongoing and provide a more quantitative analyses linking TDP-43 depletion to CUTS activation and address the reviewer’s concern regarding heterogeneity in bulk measurements. We plan to include this in a future study.

(3) Some panels in the manuscript would benefit from additional clarity to make the data easier to visualize. For example, Figure 2D and 2G could be presented in a more clear manner, possibly split into additional graphs since there are too many outputs.

We thank the reviewer for this suggestion. In response, we have split the graphs previously shown in Figures 2D and 2G to improve clarity, as we agree that these panels contained an extensive amount of data. We Specifically split Figure 2D into two separate graphs showing TDP-43 and GFP pixel intensity from Western blots on the Y-axis, plotted against low siTDP-43 treatment on the X-axis. Please see this data as Figure 2 D and Figure 2E in the new manuscript.

Furthermore, for Figure 2G we also split into graphs showing the fold change of mRNA for TDP-43 and the CUTS cryptic exon plotted against low siTDP-43 treatment on the X-axis. Please see this data as Figure 2 H and Figure 2I in the new manuscript. We have maintained the previous graphs in Supplementary Figure 2 to preserve the full dataset for reference.

(4) Sup Figure 2A image panels would benefit from being labeled, its difficult to tell what antibodies or fluorophores were used. Same with Figure 4B.

We appreciate the reviewer’s careful observation. In both figures, we are showing mCherry and GFP signals. In the revised version, we have added the corresponding labels to the side of each image for clarity. Therefore, Sup Figure 2A has been moved and is now Sup Figure 3A, while Figure 4B remains in its original configuration.

(5) Figure 3 is an important addition to this manuscript and in general is convincing showing that TDP43 loss of function mutants can alter the sensor. However, there is still wild-type endogenous TDP-43 in these cells, and it's unclear whether the 5FL mutant is acting as a dominant negative to deplete the total TDP-43 pool, which is what the data would suggest. This could have been clarified.

The TDP-43 5FL variant exhibits reduced RNA-binding capacity, and we previously demonstrated that impaired RNA binding promotes aberrant homotypic phase separation of TDP-43. Consistent with this mechanism, expression of RNA-binding–deficient TDP-43 variants induces the formation of nuclear “anisomes” which have been shown to sequester endogenous TDP-43 into insoluble fractions via dominant-negative mechanisms (Cohen et al., 2015; Keating et al., 2023; Mann et al., 2019; Yu et al., 2021). These findings support a model in which disruption of RNA engagement alters TDP-43 biophysical behavior and promotes functional depletion through self-association. We have expanded this mechanistic explanation in the Results section of the revised manuscript to better contextualize the behavior of the 5FL construct and its impact on endogenous TDP-43.

(6) Additional treatment with stressors that inactivate TDP-43 could be tested in future studies.

We appreciate this suggestion and agree with this important point. Due to the lack of methods to directly induce endogenous TDP-43 aggregation and loss of function, the use of stressors has become a partial solution to address this issue. In line with this, our group has tested several stressors in follow-up research, including sodium arsenite (NaAsO₂), puromycin, KCl, MG132, sorbitol, and tunicamycin, using HEK cells expressing the CUTS system(Xie et al., 2025). We were able to show a dose-response relationship in relative GFP intensity under these conditions, with sodium arsenite showing the strongest effect, consistent with previous reports(Huang et al., 2024). To provide additional relevant findings in the current manuscript, we expanded this analysis by testing sodium arsenite in the CUTS system while also including endogenous cryptic exons. We therefore added a new figure showing the effect of sodium arsenite on the CUTS system, including GFP intensity measurements, qPCR using CUTS cryptic exon primers, and three endogenous cryptic exon reporters (ATG4B, GPSM2, and KCNQ2).

Overall, the authors definitely achieved their goals by developing a very sensitive readout for TDP-43 function. The results are convincing, rigorous, and support their main conclusions. There are some minor weaknesses listed above, chief of which is the use of flow sorting to improve the data analysis. But regardless, this study will have an immediate impact for those who need a rapid, reliable, and sensitive assessment of TDP-43 activity, and it will be particularly impactful once this reporter can be used in isolated primary cells (ie neurons) and in vivo in animal models. Since TDP-43 loss of function is thought to be a dominant pathological mechanism in ALS/FTD and likely many other disorders, having these types of sensors is a major boost to the field and will change our ability to see sub-threshold changes in TDP-43 function that might otherwise not be possible with current approaches.

(7) Regarding the methods, they seem a bit sparse and would benefit from additional detail. For example, I do not see a section in the methods where microscopy images were quantified (%GFP positive cells for example). This information is important and is lacking in the current form.

We thank the reviewers, and we add the following information in the method section: For live imaging quantification, we measured the mean GFP signal intensity for each group. The values were averaged, and the fold change was calculated and plotted. For immunofluorescent imaging, we first created maximum intensity projection images. We then applied masks to the GFP, mCherry, and Hoechst signals. By overlapping the GFP and mCherry signals, we identified the number of GFP-positive cells. Similarly, by overlapping the mCherry signal with the Hoechst mask, we identified the CUTS-expressing cells. We then calculated the ratio of GFPpositive cells to CUTS-expressing cells and plotted it as a percentage of GFP-positive cells. All analyses were performed using the Nikon NIS software. This information is included in the methods of the revised manuscript.

Reviewer #3 (Public review):

The DNA and RNA binding protein TDP-43 has been pathologically implicated in a number of neurodegenerative diseases including ALS, FTD, and AD. Normally residing in the nucleus, in TDP-43 proteinopathies, TDP-43 mislocalizes to the cytoplasm where it is found in cytoplasmic aggregates. It is thought that both loss of nuclear function and cytoplasmic gain of toxic function are contributors to disease pathogenesis in TDP-43 proteinopathies. Recent studies have demonstrated that depletion of nuclear TDP-43 leads to loss of its nuclear function characterized by changes in gene expression and splicing of target mRNAs. However, to date, most readouts of TDP-43 loss of function events are dependent upon PCR-based assays for single mRNA targets. Thus, reliable and robust assays for detection of global changes in TDP-43 splicing events are lacking. In this manuscript, Xie, Merjane, Bergmann and colleagues describe a biosensor that reports on TDP-43 splicing function in real time. Overall, this is a well described unique resource that would be of high interest and utility to a number of researchers. Nonetheless, a couple of points should be addressed by the authors to enhance the overall utility and applicability of this biosensor.

(1) While the rationale for selecting UNC13A CE as the reporting CE species is understood given the relevance to disease, could the authors please comment on whether other CE sequences would behave similarly or as robustly? This is particularly critical given the multitude of different splicing changes that can occur as a result of TDP-43 loss of function (ie cryptic exons of differing sensitivity, skiptic exons, premature polyadenylation).

We thank the reviewer for this question regarding generalizability beyond the UNC13A CE. While UNC13A was selected due to its strong disease relevance and well-characterized sensitivity to TDP-43 loss-of-function (LOF), our platform is not intrinsically restricted to this sequence. In the manuscript, we directly compared three architectures: UNC13A-TS, CFTR-TS, and the combined CUTS sensor incorporating additional UG motif optimization. Under matched conditions in stable HEK293 lines, CUTS demonstrated superior specificity and sensitivity, exhibiting near-zero baseline activity and a proportional, log-linear response across low-dose siTDP43 (38–1200 pM) (Figures 1–2). Importantly, this head-to-head comparison demonstrates that sensor performance can be engineered and optimized beyond a single CE species.

TDP-43 LOF is known to induce a spectrum of RNA processing defects, including cryptic exons with differing sensitivities and cell-type dependence, premature polyadenylation events (e.g., STMN2), and, under conditions of excess nuclear TDP-43, exon skipping (“skiptic exons”). This diversity supports the concept in which alternative CE elements, or other TDP-43 regulated RNAs, can be incorporated into the same sensor backbone and tuned for specific biological scenarios (cell type, specific stress responses, etc...). Consistent with this, the recently described TDP-REG system (Wilkins et al., 2024) designed and AI-generated de novo CE sequences to express reporters or gene payloads, and screened multiple candidates to identify the appropriate RNA elements required for this response. These findings demonstrate that CE sequences beyond UNC13A can serve as robust TDP-43 sensing elements when optimized. Our results complement this work by demonstrating that CUTS achieves tight baseline control and a steep dynamic range (>110,000-fold induction over baseline in HEK293 cells), while maintaining compatibility across both non-neuronal and neuronal model systems, as shown in the revised manuscript.

In the revised manuscript, we show direct comparisons indicating that CUTS outperforms single-CE sensors such as UNC13A-TS and CFTR-TS under identical conditions. This supports independent work from other groups that alternative CE sequences can be engineered into effective sensors, depending on their paradigm and model systems. We have clarified this in the revised Discussion and now note that CUTS is adaptable to alternative CE inserts.

(3) Could the authors provide evidence of the utility of their biosensor in disease relevant systems that do not rely on TDP-43 KD? For example, does this biosensor report on TDP-43 loss of function in C9orf72 iPSNs in a time-dependent manner? Alternatively, groups have modeled TDP-43 proteinopathy in wildtype iPSNs via MG132 treatment.

We thank the reviewer for this important suggestion. We agree that demonstrating CUTS responsiveness in disease-relevant models independent of artificial TDP-43 knockdown would further strengthen its translational relevance. In the current study, our primary objective was to establish the sensitivity, dynamic range, and autoregulatory properties of the CUTS circuit under controlled perturbation of TDP-43 levels. siRNA-mediated depletion provides a reliable approach to establish the relationship between graded TDP-43 LOF and the CUTS sensor sensitivity/specificity. That said, CUTS is designed to detect functional TDP-43 loss irrespective of the upstream cause. As the reviewer notes, disease-relevant systems, such as C9orf72 iPSC-derived neurons and proteotoxic stress paradigms (e.g., MG132-induced impairment of TDP-43 nuclear function), are important for future studies. We are currently evaluating CUTS in iPSC-derived neuronal models of TDP-43 proteinopathy, but are optimizing the induction system, promoters, and timing. It should be noted that C9orf72 iPSC neurons do not exhibit TDP-43 LOF using standard differentiation protocols. Regarding pharmacological stress, we have shown that acute sodium arsenite treatment can activate CUTS (Figure 3). In a concurrent study under revision, we show that MG132 similarly causes TDP-43 LOF and CUTS activation (Xie et al., 2025). Notably, none of these induce complete nuclear loss of TDP-43; instead, they show nuclear TDP-43 retention or modest mislocalization. This suggests that TDP-43 LOF may also result from nuclear redistribution and dysfunction under these stress conditions, rather than from complete nuclear loss. We look forward to presenting these ongoing studies in the future.

References

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Author Response:

The following is the authors’ response to the previous reviews

Public Review:

Reviewer #1 (Public review):

The weaknesses are in the clarity and resolution of the data that forms the basis of the model. In addition to general whole embryo morphology that is used as evidence for CE defects, two forms of data are presented, co-expression and IP, as well as a strong reliance on IF of exogenously expressed proteins. Thus, it is critical that both forms of evidence be very strong and clear, and this is where there are deficiencies; 1) For vast majority of experiments general morphology and LWR was used as evidence of effects on convergent extension movements rather than keller explants or actual cell movements in the embryo. 2) the microscopy would benefit from super resolution microscopy since in many cases the differences in protein localization are not very pronounced. 3) the IP and Western analysis data often shows very subtle differences, and some cases not apparent.

Major points.

(1) Assessment of CE movement

The authors conducted an analysis of the subcellular localization of PCP core proteins, including Vangl2, Pk, Fz, and Dvl, within animal cap explants (ectodermal explants). The authors primarily used the length-to-width ratio (LWR) to evaluate CE movement as a basis for their model. However, LWR can be influenced by multiple factors and is not sufficient to directly and clearly represent CE defects. While the author showed that Prickle knockdown suppresses animal cap elongation mediated by Activin treatment, they did not test their model using standard assays such as animal cap elongation or dorsal marginal zone (DMZ) Keller explants. Furthermore, although various imaging analyses were performed in Wnt11-overexpressing animal caps and DMZ explants, the Wnt11-overexpressing animal caps did not undergo CE movement. Given that this study focuses on the molecular mechanisms of Vangl2 and Ror2 regulation of Dvl2 during CE, the model should be validated in more appropriate tissues, such as DMZ explants.

(2) Overexpression conditions

Another concern is that most analyses were performed with overexpression conditions. PCP core proteins (Vangl2, Pk, Dvl, and Fz receptors) are known to display polarized subcellular localization in both the neural epithelium and DMZ explants (Ref: PCP and Septins govern the polarized organization of the actin cytoskeleton during convergent extension, Current Biology, 2024). However, in this study, overexpressed PCP core proteins failed to show polarized localization. Previous studies, such as those from the Wallingford lab, typically used 10-30 pg of RNA for PCP core proteins, whereas this study injected 100-500 pg, which is likely excessive and may have created artificial conditions that confound the imaging results.

(3) Subtle and insufficient effects

Several of the reported results show quite modest changes in imaging and immunoprecipitation analyses, which are not sufficient to strongly support the proposed molecular model. For example, most Dvl2 remained localized with Fz7 even under Vangl2 and Pk overexpression (Fig. 4). Similarly, Wnt11 overexpression only slightly reduced the association between Vangl2 and Dvl2 (Sup. Fig. 8), and the Ror2-related experiments also produced only subtle effects (Fig. 8, Sup. Fig. 15).

We thank reviewer 1 for careful reading of our revised manuscript, and additional constructive criticisms. Since the two reviewers had divergent opinions towards our revised manuscript, we think that it might be more productive to request a Version of Record at this point, and have our proposed model debated/ tested by others in the field. We will keep the reviewer’s suggestions in mind while design ongoing studies. We would like to address the criticisms collectively below:

(1) The primary goal of our current manuscript is to build a mechanistic model for non-canonical Wnt signaling through elucidating the functional relationships between Dvl, Vangl, PK and Ror during CE. They each have been studied extensively in prior literature using DMZ injected embryos, and DMZ, Keller and animal cap explants, so there is little doubt that the reduced LWR following their over-expression or knockdown in DMZ is due to disruption of CE. In the context of our study in the current manuscript, we primarily performed their co-injections in different combinations to differentiate synergistic vs. antagonistic relationship, and in the majority cases we relied on epistatsis to draw conclusions (e.g. Fig. 1; Fig. 2h, I; Suppl. Fig. 6; Suppl. Fig. 14). Nevertheless, we did follow the reviewer’s suggestion and used animal cap elongation as an additional assay to confirm that Pk and Vangl2 did synergize to disrupt CE, and their synergy could be blocked by Dvl2 co-overexpression; the new data is added to Fig. 1 (Fig. 1h, h’). Therefore, given the prior literature, our new animal cap explant data, and the specific scope of our current study, we feel that the LWR measurement is a reasonable assay to determine CE phenotype in this manuscript. We fully agree with the reviewer that our model will need to be tested at the cellular level through live imaging of DMZ explants; it is indeed the direction of our future study, but is beyond the scope of the current manuscript.

(2) A salient feature of non-canonical Wnt signaling is that loss or over-expression of any components can often cause identical CE defects at the tissue/ embryo level. We used many co-injection experiments to demonstrate that this is due, at least in part, to a counterbalance between Dvl/Ror and Vangl/PK (e.g. Fig. 1; Fig. 2h, I; Suppl. Fig. 6; Suppl. Fig. 14). It is in this context that we planned the imaging and biochemical experiments to determine the possible molecular mechanisms underlying their functional interaction, and we feel that the moderate over-expression used is reasonable in this case for us to build the first integrated model. We do plan to test our model using lower expression in the future. To acknowledge the limitation of our study, we also added the following sentences in the Discussion:

“We acknowledge, however, that our model explains primarily the potential molecular actions underlying the regulation of CE at the tissue level. Whether and how our model may explain the cellular behavior during CE, such as polarized remodeling of cell junction or extension of cell protrusions, will require further study.”

(3) The Wnt11 induced reduction of Dvl2-Vangl2 co-IP (Suppl. Fig. 8, 15) may be moderate, but is statistically significant and reproducible, and we have reported similar findings in two other publications (DOI: 10.1093/hmg/ddx095; DOI: 10.1038/s41467-025-57658-0). Given the limitation of co-IP, we had to rely on high level over-expression to make the experiments feasible. We are building proximity based assays such as NanoBRET, and plan to verify the result with lower level expression in the future.

Reviewer #2 (Public review):

We thank the reviewer for the encouraging comments, and the suggestion to clarify the description related to Suppl. Fig. 15. We made revision according to the reviewer’s suggestion, and added Suppl. Fig. 16 to further examine the effect of Ror2 knockdown on the steady state interaction between Dvl2 and Vangl2 using imaging approach.

Unfortunately, we are animals. We don't live off the sun's rays and water and simply kill out of competition for non-living resources, we eat other living things. Jains put great effort into not killing living things (don't eat root vegetables for example), but that severely impacts their lives.

Being vegan I have a couple ways I think about the violence of my life. Mainly, I honestly don't think it has changed MY life much at all to be vegan, yet it has changed the lives of the many animals impacted by eating animal products regularly. * From an energy perspective, eating plants takes less lives simply because the animal I may eat had to eat something as well, and energy is lost as it goes through that cycle of eating. This is unchangeable right now. * The difficulties with being vegan aren't really because of the lifestyle itself, it's because of greater society. Society allows me to live a vegan lifestyle, in that I can easily get the nutrients I need from the grocery store's options (there is an abundance of food). Society also makes it difficult to be vegan because most available dishes and processed foods use animal products unnecessarily, it is simply the dominant way of living that perpetuates itself. I don't view that inconvenience as important to me, because it is simply a structural problem. * The Jain lifestyle at its most extreme kind of consumes one's life. Not being able to take a step without brushing potential bugs out of the way on the ground makes it difficult to merely exist. Perhaps it is the way of living that reduces suffering the most, but at what cost to you? Veganism doesn't require so much change in ways of living, just choices.

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Reply to the reviewers

Reviewer #1

Figure 1D: It would be useful to indicate the number of embryos analyzed for these experiments (n = ?).

Number of embryos now included in figure legend

Figure 3B: The control condition for gcl⁻/⁻; ras-RNAi is labeled as "EV". This terminology (presumably "empty vector") is not defined in either the text or the figure legend. In addition, the magenta channel for the Ras-G37 condition appears to be flipped horizontally.

We replaced with “-“ in figure and figure legend

Page 7: The text states that "Ras-C40 activates the PI3K pathway," whereas the figure depicts Ras-C40 as activating the RalA pathway. This discrepancy could be confusing for the reader and should be corrected.

The diagram has been corrected

Figures 4 and 5: To facilitate interpretation, it may be helpful to include a schematic of the PI3K complex indicating the different subunits used in the study, along with information (potentially color-coded) about whether each construct primarily acts as an activator or inhibitor of PI3K function.

Figure 4E and Figure 5E were added

Figure 4A and 4B: For clarity and consistency with the text, the panels (and corresponding plots) for dp110-WT and dp110-CAAX could be placed before those for dp110-D954A and dp110-ΔRBD.

Order of constructs was rearranged

Figure 5C: The term "p60-TCEp3," which appears to correspond to the germ plasm-targeted p60-WT construct, is not defined in either the figure legend or the main text.

Clarification was added to the text (p.11, line 225)

Page 12: The reference "(Fig. S1A, Movie 1)" should be corrected to "(Fig. S2A, Movie 1)."

Corrected

Page 13: There is a missing word in the sentence "the biosensor appeared to be enrich to...", which should be corrected to "enriched."

Corrected

Figure 7A: Although the data presented are interesting and ultimately support the authors' conclusion that Torso regulates PIP3 levels, the results are somewhat counter-intuitive and may be confusing for readers. The authors might consider moving this panel to the Supplementary Figures. In addition, it could be informative to include PIP3 measurements for gcl⁻/⁻ (and possibly gcl⁺/⁻) pole buds in Figure 7B, as PIP3 appears particularly enriched in these conditions compared to wild type.

We agree that at first the findings in the early embryos were confusing, but we prefer including them in the main figure to demonstrate changes in PIP 3 distributions in torso mutants. We are now providing a possible explanation for these findings (p13 line 270-). The differences are quite clear in the older embryos and measurements shown in 7B-D. Pole bud measurements for gcl-/- and gcl+/- are shown in figure 6 E-G.

Reviewer #2

Fig. legends to 1C and 1D are swapped.

Corrected

Why is csw not necessary for PGC formation? It acts upstream of Ras. This is not discussed.

We now highlight this point in the text (and refer to studies on the sevenless kinase, which suggested a similar position of Csw parallel or downstream of Ras (page 6 line 107-).

Fig 3C. Consider changing the order of the ras-variants used: S35, G37, C40 instead of S35, C40, G37.

We changed the schematic in Figure 3C that should make the order of Ras variants more intuitive.

Fig 4A, B: Consider changing the order of the panels. Control, dp110-wt, dp110-CAAX, dp110-D954A, dp110-deltaRBD.

Order of constructs was rearranged

Fig S4 is mentioned in the text before S2 and S3. Consider changing the suppl. figure order.

Order of supplementary figures was rearranged

Page 12: Fig S1 A does not show PIP2 dynamics. Movie 1 is not available to this reviewer. The authors most likely refer to fig. S2.

Movie 1 was uploaded and figure calls were corrected

Page 13, 1st para: Why do the authors use glc heterozygous embryos to look at PIP3 and PIP2? Particularly so when they report later in the MS that glc+/- behave differently to wt controls in terms of PIP3 levels (Fig. 7C). By looking at gcl+/+, they might find that now PIP2 levels are different in gcl mutant embryos or that the differences between PIP3 levels in +/+ and -/- are larger than compared with +/-.

Since gcl+/- embryos form the same number of PGCs as WT but show a statistically significant increase in PI3K activity when comparing membrane to cytoplasm staining intensity, we favor using gcl+/- embryos, as these embryos may represent a more sensitive test for PIP2 and PIP3 levels.

Pages 15 and 16: revise figure calls in the text.

Figure calls were revised

M+M: How were gcl+/- and gcl-/- embryos identified?

Since all genetic manipulations in this alter the maternal contribution to the embryo, we us the term ‘mutant’ embryos referring to the maternal genotype (indicated on page 3 line 33 and more clearly stated in material and methods and reagent table). Embryos derived from mother of a specific maternal genotype are all identical, thus we can easily distinguish between embryos derived from homozygous mutant mothers (gcl-/-) or heterozygous mutant mothers (gcl-/+) In the reagents table we include the precise genotype description. “CyO” refers to the balancer chromosome commonly used to identify heterozygotes on the second chromosome. Flies with the CyO balancer have curly wings.

Reviewer #3

Figure 1B: The authors describe that embryos with OptoSos still form buds which protruded from the cortex, but PGCs largely fail to cellularize (described in pg. 5). I'm not sure what they meant by "fail to cellularize" as this is not obvious to me when looking at the figure. The authors should describe how they know it's cellularized in the controls and not in the OptoSos or change the wording to "suggesting a failure to cellularize".

We used the word ‘protruded’ to describe our live observations. PGCs were quantified in fixed embryos, immunostained with anti-Vasa antibody to count Vasa positive cells (Fig 1C and D. We observe a lack of Vasa-positive PGCs, only in the light-activated OptoSos condition.

Fig. 1B, lines 4-5: at what stage are these embryos? Cycle 9? Cycle 14? Both?

Nuclear cycles of embryos for each panel are noted on the left side of each panel

Fig. 4A: add dp110-CAAX results to Results section

dp110-CAAX results are included in the Results section (p.9. line 177)

Figure 5C: The hyper-clustered phenotype they describe is hard to visualize in this figure (described in pg. 11). The authors should describe what is meant by "hyper-clustered".

We agree and re-worded the description of this observation to be clearer, page 11, line 226-.

Figure 7: When comparing Fig. 7A and 7B torsoHH/WK images, we can see that in Fig. 7A that PIP3 pattern changes such that PIP3 is now at the most posterior end where PGC will eventually form (compared to control that has low PIP3 in this region), but then in Fig. 7B they are looking at the buds and they say PIP3 levels decrease, which does not correspond to Fig. 7A. Are these simply different stages and PIP3 levels change over time (looking at Fig. 7C, PIP3 does not seem to change a lot over time)?

The figure legend now states more clearly that embryos were of different ages. We also explain in the text the apparent discrepancy in the patterns before and during budding (page13 line 266). The time points in figure 7C span nuclear cycle 10, not earlier (page14 line 274). By measuring membrane to cytoplasmic distribution, a more accurate comparison is possible at this stage.

p. 5, line 5: "Optosos" is written "OptoSos" elsewhere (suggest using OptoSos throughout)

Corrected

Is it possible that inhibition of myosin II recruitment is due to conversion of PIP2 -> PIP3, thus loss of PIP2, or is it that myosin is specifically recruited to regions where PIP2 is high? This seems like a point that should be added to the discussion.

This point is now discussed on page 20, line 403

p. 5, line 6: suggest adding a comma after "Ras" for clarity

Corrected

p. 5, last line: the genotype is "w^1118" (with ^ indicating a superscript), not "w^-1118", and is italicized (this should be corrected throughout)

Corrected

p. 6, line 2: replace "cellularizing" with "cellularization"

Corrected

p. 6, lines 11-13: Where is it shown that knockdown of csw, dsor1 and rolled did not restore PGC formation? The data are not present in Fig. 2C (could include in supp fig?)

We added these data as Supplementary figure 1

p. 7, line 1: replace "interfere" with "interferes"

Corrected

p. 7, last three lines: what is stated here, "Ras-G37 [activates] both the RalA and the PI3K pathways, and Ras-C40 activates the PI3K pathway" is not consistent with what is diagrammed in Fig. 3C, where Ras-C40 is indicated as activating RalA (please correct either the text or the diagram)

We apologize and corrected the figure

p. 11, lines 1-2: the Pi3K21B gene and transcript should be italicized (note that Pi3K21B is the official gene name on FlyBase)

Gene name was italicized

p. 11, lines 6-10: it might be helpful to explain how the p60 construct was overexpressed (current lines 9-10) before describing the results (current lines 7-8)

Clarification on p60 construct was added to p.11, line 215-

p. 12, paragraph 2, line 2: the PIP2 biosensor should be written as "PLCgamma[PH]:mCherry" throughout, not "PLCy[PH]:mCherry"; this should be changed in the figures as well as the text (Symbol font can be used to turn "g" into lower-case "gamma", both in Word and in Illustrator)

Gamma symbol was added

It would also be helpful to show the overlap of the PIP2 and PIP3 signals in control vs. gcl mutants at different stages so the relative distribution and intensity of the signals can be better appreciated (consider adding this as a supplementary figure).

Our data show that PIP2 is not affected by lack of GCL (Fig 6 B-D). We thus do not think that simultaneous imaging of PIP2 and PIP3 in gcl-/- would add to our conclusions. Furthermore, these experiments would require a significant time investment to generate the respective genotypes. Thus, we agree with the reviewer that this is experiment is beyond the scope of the paper.

p. 12, paragraph 2, line 3: it does not appear that the two PIP markers were used "simultaneously" in Fig. 6A; however, this is evident from Fig. S2 and Movie 1 (consider placing callouts to these earlier in the paragraph or moving the description of simultaneous expression and observation of the two markers later in the paragraph to avoid confusion)

We did simultaneously image PIP2 and PIP3 sensors and have added this as Movie 1 and also in supplementary Figure S4, which are now clearly referred to in the text.

p. 12, paragraph 2, line 7: replace "Fig. S1A" with "Fig. S2" (this was confusing)

Figure call was updated

p. 16: change "Fig. 7G-I" to "Fig. 8G-I"

Figure call was updated

p. 20, Deming reference: there appears to be a stray asterisk in the title

Asterisk was removed from reference

Fig. 1D: need to explain that the colors in the graph indicate the numbers of PGCs formed (this could also be added as a label across the top of the graph); in addition, the number of embryos examined for each genotype should be included in the legend

We added a label at the top of the graph and ‘n’ were added to figure legend

Fig. 2B: spell out where csw, dsor1 and rolled data are shown; also, "n" is not defined; was this the number of embryos per genotype?

We added these data as Supplemental Figure 1

Fig. 3B: "EV" should be defined in the legend; is this "empty vector"?

We are using a “-“ to mark controls without transgene

Fig. 3C: see previous comment re: mistake in the diagram; I believe Ras-C40 was described as activating PI3K, not RalA

We apologize and corrected the figure

Fig. 4B, line 2: was the graph plotted from the data in panel (C) or panel (A)? panel (A) seems more likely, because the data in C is plotted in D; please correct the panel callout

Figure legend was updated to refer to the correct panel

Fig. 5C: describe "p60-TCEp3" in the legend

We added germplasm-targeting 3’UTR (TCEp3) to legend and the construct and reference are provided in Material and Methods section

Figure 6: In Fig. 6E-G, the "brightness" of PIP3 at the membrane corresponds to the images even with different views (posterior and orthogonal) and agrees with the graph.

However, when looking at Fig. 6B, it looks to me that PIP2 is brighter in gcl+/-, but the opposite is true when looking at Fig. 6D (i.e., PIP2 looks brighter in gcl-/-). The authors might want to comment on this.

We have updated the figure to better reflect our observations.

Fig. 6A: define "(fire)" here or in the first figure legend where this is used

We added an inset for the fire lookup table to clearly define the pseudcolor scheme used in the image

Figure 8 title: "Actin fluorescence is increased in gcl-/- pole buds",But their graph in Fig. 8B comparing actin in gcl+/- to -/- is not significant

Thanks for catching our mistake, myosin not actin is changed

Fig. 8I: replace "Scarlett" with "Scarlet"

Corrected

Fig. 8D-F: Although the plots in panel E agree with the images in panel D, it is unclear why those in panel F are not more concordant. In F, myosin appears enriched at the cortex relative to the cytoplasm in gcl-/- mutants, which is hard to reconcile with the data in D-E.

We have updated the figure to better reflect our observations.

Fig. S2A: define the three time points shown here, and clarify that these are shown left to right (if this is indeed the case)

We removed S2A and updated the movie to replace it

Fig. S4: change "P60" to "p60" in the figure title

Corrected

Movie: The movies showing PIP2 and PIP3 in whole embryos are nice, but it would also be helpful to also include merged images of the two channels, so the reader can examine the relative accumulation of the two PIPs over time.

Merged images panel was added to the movie.

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Referee #3

Evidence, reproducibility and clarity

Summary:

Although Torso is known to antagonize primordial germ cell (PGC) formation, the underlying mechanisms remain unclear. Canonical Torso signalling typically results in activation of Ras. However, the authors show that Ras-mediated suppression of PGC formation is independent of the Raf/MEK/ERK pathway. Instead, they uncover an unexpected role for Torso in activating phosphoinositide 3-kinase (PI3K) that promotes formation of PIP3 enriched posterior membrane domains. The resulting increase in PI3K activity disrupts PGC formation. Furthermore, they show that by promoting Torso degradation, the ubiquitin ligase adaptor Germ Cell-Less (GCL) primes the posterior membrane with reduced PIP3 to facilitate PGC formation. Lastly, the authors suggest a model where antagonistic relationship between GCL and Torso influences actomyosin contractility that may allow the bud to constrict for proper PGC formation.

Major comments:

Figure 1B: The authors describe that embryos with OptoSos still form buds which protruded from the cortex, but PGCs largely fail to cellularize (described in pg. 5). I'm not sure what they meant by "fail to cellularize" as this is not obvious to me when looking at the figure. The authors should describe how they know it's cellularized in the controls and not in the OptoSos or change the wording to "suggesting a failure to cellularize".

Figure 5C: The hyper-clustered phenotype they describe is hard to visualize in this figure (described in pg. 11). The authors should describe what is meant by "hyper-clustered".

Figure 6: In Fig. 6E-G, the "brightness" of PIP3 at the membrane corresponds to the images even with different views (posterior and orthogonal) and agrees with the graph. However, when looking at Fig. 6B, it looks to me that PIP2 is brighter in gcl+/-, but the opposite is true when looking at Fig. 6D (i.e., PIP2 looks brighter in gcl-/-). The authors might want to comment on this.

It would also be helpful to show the overlap of the PIP2 and PIP3 signals in control vs. gcl mutants at different stages so the relative distribution and intensity of the signals can be better appreciated (consider adding this as a supplementary figure).

Figure 7: When comparing Fig. 7A and 7B torsoHH/WK images, we can see that in Fig. 7A that PIP3 pattern changes such that PIP3 is now at the most posterior end where PGC will eventually form (compared to control that has low PIP3 in this region), but then in Fig. 7B they are looking at the buds and they say PIP3 levels decrease, which does not correspond to Fig. 7A. Are these simply different stages and PIP3 levels change over time (looking at Fig. 7C, PIP3 does not seem to change a lot over time)?

Page 15, last paragraph: "If myosin II recruitment is inhibited when PIP3 levels are high" Is it possible that inhibition of myosin II recruitment is due to conversion of PIP2 -> PIP3, thus loss of PIP2, or is it that myosin is specifically recruited to regions where PIP2 is high? This seems like a point that should be added to the discussion.

Overall, I think their claim that antagonistic activities of GCL and Torso is crucial for PGC formation is well justified. The combination of optogenetic tools with activation and lof mutants is nicely done. Some clarification regarding the PIP3 and PIP2 levels will be helpful to the reader (see my comments above). The myosin claim is less convincing (see my comment on Fig. 8D-F below).

Minor comments on the text:

p. 5, line 5: "Optosos" is written "OptoSos" elsewhere (suggest using OptoSos throughout) p. 5, line 6: suggest adding a comma after "Ras" for clarity p. 5, last line: the genotype is "w^1118" (with ^ indicating a superscript), not "w^-1118", and is italicized (this should be corrected throughout) p. 6, line 2: replace "cellularizing" with "cellularization" p. 6, lines 11-13: Where is it shown that knockdown of csw, dsor1 and rolled did not restore PGC formation? The data are not present in Fig. 2C (could include in supp fig?) p. 7, line 1: replace "interfere" with "interferes" p. 7, last three lines: what is stated here, "Ras-G37 [activates] both the RalA and the PI3K pathways, and Ras-C40 activates the PI3K pathway" is not consistent with what is diagrammed in Fig. 3C, where Ras-C40 is indicated as activating RalA (please correct either the text or the diagram) p. 11, lines 1-2: the Pi3K21B gene and transcript should be italicized (note that Pi3K21B is the official gene name on FlyBase) p. 11, lines 6-10: it might be helpful to explain how the p60 construct was overexpressed (current lines 9-10) before describing the results (current lines 7-8) p. 12, paragraph 2, line 2: the PIP2 biosensor should be written as "PLCgamma[PH]:mCherry" throughout, not "PLCy[PH]:mCherry"; this should be changed in the figures as well as the text (Symbol font can be used to turn "g" into lower-case "gamma", both in Word and in Illustrator) p. 12, paragraph 2, line 3: it does not appear that the two PIP markers were used "simultaneously" in Fig. 6A; however, this is evident from Fig. S2 and Movie 1 (consider placing callouts to these earlier in the paragraph or moving the description of simultaneous expression and observation of the two markers later in the paragraph to avoid confusion) p. 12, paragraph 2, line 7: replace "Fig. S1A" with "Fig. S2" (this was confusing) p. 16: change "Fig. 7G-I" to "Fig. 8G-I" p. 20, Deming reference: there appears to be a stray asterisk in the title

Minor comments on the figures and figure legends:

Fig. 1B, lines 4-5: at what stage are these embryos? Cycle 9? Cycle 14? Both? Fig. 1C: see previous comment about "w^1118" genotype nomenclature Fig. 1D: need to explain that the colors in the graph indicate the numbers of PGCs formed (this could also be added as a label across the top of the graph); in addition, the number of embryos examined for each genotype should be included in the legend Fig. 2B: spell out where csw, dsor1 and rolled data are shown; also, "n" is not defined; was this the number of embryos per genotype? Fig. 3B: "EV" should be defined in the legend; is this "empty vector"? Fig. 3C: see previous comment re: mistake in the diagram; I believe Ras-C40 was described as activating PI3K, not RalA Fig. 3E: fix "w^1118" as described above Fig. 4A: add dp110-CAAX results to Results section Fig. 4B, line 2: was the graph plotted from the data in panel (C) or panel (A)? panel (A) seems more likely, because the data in C is plotted in D; please correct the panel callout Fig. 5C: describe "p60-TCEp3" in the legend Fig. 6A: define "(fire)" here or in the first figure legend where this is used Figure 8 title: "Actin fluorescence is increased in gcl-/- pole buds",But their graph in Fig. 8B comparing actin in gcl+/- to -/- is not significant Fig. 8D-F: Although the plots in panel E agree with the images in panel D, it is unclear why those in panel F are not more concordant. In F, myosin appears enriched at the cortex relative to the cytoplasm in gcl-/- mutants, which is hard to reconcile with the data in D-E. Fig. 8I: replace "Scarlett" with "Scarlet" Fig. S2A: define the three time points shown here, and clarify that these are shown left to right (if this is indeed the case) Fig. S4: change "P60" to "p60" in the figure title

Movie: The movies showing PIP2 and PIP3 in whole embryos are nice, but it would also be helpful to also include merged images of the two channels, so the reader can examine the relative accumulation of the two PIPs over time.

Referees cross-commenting

I agree enthusiastically with the comments of the other reviewers, who often came to the same conclusion I did about the manuscript and the data, including some of the detailed points about the figures, etc.

Significance

General assessment:

The many strengths of this manuscript include elegant genetic and optogenetic approaches using well-designed transgenes.

The main weakness is the lack of experiments showing simultaneous live imaging of the PIP2 and PIP3 sensors in gcl-/- and other genetic backgrounds, which would help the reader better envision how regulators of this pathway affect phospholipid distribution at the level of whole embryos and prospective pole cells. Note that because of the time required, I do not insist that they do this.

Advance:

Study demonstrates for the first time an unexpected role of Torso in PI3K regulation

Audience:

germ cell afficionados, developmental biologists, cell biologists, PI3K researchers

My field of expertise:

Drosophila, germ cell development, genetics, cell biology, live imaging, phosphoinositides

Author Response:

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

Public Reviews:

Reviewer #1 (Public review):

This manuscript investigates how dentate gyrus (DG) granule cell subregions, specifically suprapyramidal (SB) and infrapyramidal (IB) blades, are differentially recruited during a high cognitive demand pattern separation task. The authors combine TRAP2 activity labeling, touchscreen-based TUNL behavior, and chemogenetic inhibition of adult-born dentate granule cells (abDGCs) or mature granule cells (mGCs) to dissect circuit contributions.

This manuscript presents an interesting and well-designed investigation into DG activity patterns under varying cognitive demands and the role of abDGCs in shaping mGC activity. The integration of TRAP2-based activity labeling, chemogenetic manipulation, and behavioral assays provides valuable insight into DG subregional organization and functional recruitment. However, several methodological and quantitative issues limit the interpretability of the findings. Addressing the concerns below will greatly strengthen the rigor and clarity of the study.

Major points:

(1) Quantification methods for TRAP+ cells are not applied consistently across panels in Figure 1, making interpretation difficult. Specifically, Figure 1F reports TRAP+ mGCs as density, whereas Figure 1G reports TRAP+ abDGCs as a percentage, hindering direct comparison. Additionally, Figure 1H presents reactivation analysis only for mGCs; a parallel analysis for abDGCs is needed for comparison across cell types.

In Figure 1G and 1H we report TRAP+ abDGCs as a percentage rather than density because we are analyzing colocalization of the two markers, which are very sparse in this population. Given the very low number of double-labeled abDGCs, calculating density would not be practical. In the revised manuscript we have clarified the rationale for using these measures. As noted in the current text, we did not observe abDGCs co-expressing TRAP and c-Fos; we have made this point more explicit to guide interpretation of these data.

(2) The anatomical distribution of TRAP+ cells is different between low- and high-cognitive demand conditions (Figure 2). Are these sections from dorsal or ventral DG? Is this specific to dorsal DG, as it is preferentially involved in cognitive function? What happens in ventral DG?

The sections shown in Figure 2 were obtained from the dorsal dentate gyrus (see Methods, “Histology and imaging”: stereotaxic coordinates −1.20 to −2.30 mm relative to bregma, Paxinos atlas). From a feasibility standpoint, it is not possible to analyze the entire longitudinal extent of the hippocampus with these low-throughput histological approaches. We therefore focused on the dorsal DG, for which there is a strong functional rationale. A large body of work indicates that the dorsal hippocampus, and specifically the dorsal DG, is preferentially involved in spatial memory and in the fine contextual discrimination that underlies pattern separation. The dorsal hippocampus is critical for encoding and distinguishing similar spatial representations, a core component of the high-cognitive demand task used here. In contrast, the ventral DG is more strongly associated with emotional regulation and affective memory processing and is less implicated in high-resolution spatial encoding. For these reasons, the present study was designed to assess TRAP+ cell distributions specifically in the dorsal DG.

(3) The activity manipulation using chemogenetic inhibition of abDGCs in AsclCreER; hM4 mice was performed; however, because tamoxifen chow was administered for 4 or 7 weeks, the labeled abDGC population was not properly birth-dated. Instead, it consisted of a heterogeneous cohort of cells ranging from 0 to 5-7 weeks old. Thus, caution should be taken when interpreting these results, and the limitations of this approach should be acknowledged.

We agree that prolonged tamoxifen administration results in labeling a heterogeneous population of abDGCs spanning approximately 0 to 5–7 weeks of age, rather than a precisely birth-dated cohort. This is a limitation of this approach and we have included discussion of this in more detail in the revised manuscript.

(4) There is a major issue related to the quantification of the DREADD experiments in Figure 4, Figure 5, Figure 6, and Figure 7. The hM4 mouse line used in this study should be quantified using HA, rather than mCitrine, to reliably identify cells derived from the Ascl lineage. mCitrine expression in this mouse line is not specific to adult-born neurons (off-targets), and its expression does not accurately reflect hM4 expression.

We agree that mCitrine is not a marker that allows localization of hM4Di as it is well known that the mCitrine can be independently expressed in a Cre independent manner in this mouse. As suggested, we have removed the figure that showed the mCitrine and have performed immunohistochemical localization of the DREADD with an antibody against the HA tag. This is now shown in Figure 5.

(5) Key markers needed to assess the maturation state of abDGCs are missing from the quantification. Incorporating DCX and NeuN into the analysis would provide essential information about the developmental stage of these cells.

The goal of this study was to examine activity patterns of adult-born versus mature granule cells, rather than to assess maturation state. The adult-born neurons analyzed were 25–39 days old, an age at which point most cells have progressed beyond the DCX⁺ stage and are expected to express NeuN based on prior work. We therefore do not think that including DCX or NeuN quantification would provide additional information relevant to the aims or interpretation of this study.

Minor points:

(1) The labeling (Distance from the hilus) in Figure 2B is misleading. Is that the same location as the subgranular zone (SGZ)? If so, it's better to use the term SGZ to avoid confusion.

We have updated Figure 2B, the Methods, and the main text to more explicitly localize this which it the boundary between the subgranular zone (SGZ) and the hilus.

(2) Cell number information is missing from Figures 2B and 2C; please include this data.

We have now added the cell number information to the figure legends. In Figures 2B and 2C, each point corresponds to a single cell, with an equal number of mice per group. The total number of TRAP⁺ cells per mouse is shown in Figure 1F, which reports TRAP⁺ cell densities by group.

(3) Sample DG images should clearly delineate the borders between the dentate gyrus and the hilus. In several images, this boundary is difficult to discern.

We made the DG-hilus boundaries clearer in the sample images to improve visualization and interpretation.

(4) In Figure 6, it is not clear how tamoxifen was administered to selectively inhibit the more mature 6-7-week-old abDGC population, nor how this paradigm differs from the chow-based approach. Please clarify the tamoxifen administration protocol and the rationale for its specificity.

We apologize for the confusion here. The protocol used in Figure 6 is the same tamoxifen chow–based approach as in Figure 5, differing only in the duration of tamoxifen exposure. Mice in Figure 5 received tamoxifen chow for 7 weeks, whereas mice in Figure 6 received it for 4 weeks, restricting labeling to a younger and narrower cohort of adult-born DGCs. Thus, the population targeted in Figure 6 is younger than that in Figure 5 and does not correspond to mature 6–7-week-old neurons. By contrast, the experiment in Figure 4 targets a more mature population, consisting predominantly of ~5-week-old adult-born neurons as well as mature granule cells, which are Dock10-positive and express Cre endogenously, allowing selective manipulation of this later-stage population.

We have corrected the paragraph accordingly and clarified the age range of the labeled populations in the revised manuscript.

Reviewer #2 (Public review):

Summary

In this manuscript, the authors combine an automated touchscreen-based trial-unique nonmatching-to-location (TUNL) task with activity-dependent labeling (TRAP/c-Fos) and birth-dating of adult-born dentate granule cells (abDGCs) to examine how cognitive demand modulates dentate gyrus (DG) activity patterns. By varying spatial separation between sample and choice locations, the authors operationally increase task difficulty and show that higher demand is associated with increased mature granule cell (mGC) activity and an amplified suprapyramidal (SB) versus infrapyramidal (IB) blade bias. Using chemogenetic inhibition, they further demonstrate dissociable contributions of abDGCs and mGCs to task performance and DG activation patterns.

The combination of behavioral manipulation, spatially resolved activity tagging, and temporally defined abDGC perturbations is a strength of the study and provides a novel circuit-level perspective on how adult neurogenesis modulates DG function. In particular, the comparison across different abDGC maturation windows is well designed and narrows the functionally relevant population to neurons within the critical period (~4-7 weeks). The finding that overall mGC activity levels, in addition to spatially biased activation patterns, are required for successful performance under high cognitive demand is intriguing.

Major Comments

(1) Individual variability and the relationship between performance and DG activation.

The manuscript reports substantial inter-animal variability in the number of days required to reach the criterion, particularly during large-separation training. Given this variability, it would be informative to examine whether individual differences in performance correlate with TRAP+ or c-Fos+ density and/or spatial bias metrics. While the authors report no correlation between success and TRAP+ density in some analyses, a more systematic correlation across learning rate, final performance, and DG activation patterns (mGC vs abDGC, SB vs IB) could strengthen the interpretation that DG activity reflects task engagement rather than performance only.

As mentioned, we previously reported no correlation between task success and TRAP+ density. We have now performed additional analyses examining correlations with learning rate, final performance, and DG activation patterns (mGC vs abDGC, SB vs IB), and found no significant relationships. Therefore, as we did not find any positive correlations the original interpretation that DG activity primarily reflects task engagement rather than performance level seems the most parsimonious.

(2) Operational definition of "cognitive demand".

The distinction between low (large separation) and high (small separation) cognitive demand is central to the manuscript, yet the definition remains somewhat broad. Reduced spatial separation likely alters multiple behavioral variables beyond cognitive load, including reward expectation, attentional demands, confidence, engagement, and potentially motivation. The authors should more explicitly acknowledge these alternative interpretations and clarify whether "cognitive demand" is intended as a composite construct rather than a strictly defined cognitive operation.

We agree that reducing spatial separation between stimuli likely engages multiple behavioral and cognitive processes beyond a single, strictly defined operation. We have now clarified this point in the manuscript and explicitly state that our use of the term “cognitive demand” reflects a multidimensional behavioral challenge rather than a singular cognitive process (see Discussion).

(3) Potential effects of task engagement on neurogenesis.

Given the extensive behavioral training and known effects of experience on adult neurogenesis, it remains unclear whether the task itself alters the size or maturation state of the abDGC population. Although the focus is on activity and function rather than cell number, it would be useful to clarify whether neurogenesis rates were assessed or controlled for, or to explicitly state this as a limitation.

While the primary goal of this study was to examine activity and functional recruitment of adult-born granule cells, we also quantified the survival of birth-dated neurons at the end of behavioral training. Density measurements of BrdU⁺ and EdU⁺ cells revealed no differences across experimental groups, indicating that engagement in the pattern separation task, across low to high cognitive demand conditions, did not significantly alter survival of adult-born neurons. In addition, we examined the spatial distribution of BrdU⁺ and EdU⁺ neurons between the suprapyramidal and infrapyramidal blades of the dentate gyrus. The proportion of newborn neurons was consistent across all groups, with approximately 60% located in the suprapyramidal blade and 40% in the infrapyramidal blade. These findings indicate that behavioral training did not alter the baseline distribution of adult-born neurons. We have now clarified these points in the manuscript (See Results).

(4) Temporal resolution of activity tagging.

TRAP and c-Fos labeling provide a snapshot of neural activity integrated over a temporal window, making it difficult to determine which task epochs or trial types drive the observed activation patterns. This limitation is partially acknowledged, but the conclusions occasionally imply trial-specific or demand-specific encoding. The authors should more clearly distinguish between sustained task engagement and moment-to-moment trial processing, and temper interpretations accordingly. While beyond the scope of the current study, this also motivates future experiments using in vivo recording approaches.

We agree and have made changes to the manuscript to discuss these points (see Discussion and Limitations).

(5) Interpretation of altered spatial patterns following abDGC inhibition.

In the abDGC inhibition experiments, Cre+ DCZ animals show delayed learning relative to controls. As a result, when animals are sacrificed, they may be at an intermediate learning stage rather than at an equivalent behavioral endpoint. This raises the possibility that altered DG activation patterns reflect the learning stage rather than a direct circuit effect of abDGC inhibition. Additional clarification or analysis controlling for the learning stage would strengthen the causal interpretation.

We agree that differences in learning stage could in principle confound the interpretation of DG activation patterns. However, although Cre+ DCZ-treated mice exhibited delayed learning, they ultimately reached the same performance criterion as control animals. Thus, adult-born DGC inhibition did not prevent learning but increased the time required to reach criterion, indicating that these neurons are beneficial for learning efficiency rather than strictly necessary for task acquisition. Importantly, all animals were sacrificed only after reaching the predefined success criterion. Therefore, the immunohistochemical analyses were performed at the same behavioral endpoint for Cre+ DCZ and control groups, even though the number of training days differed. Consequently, the observed differences in DG activation reflect circuit recruitment at equivalent task mastery rather than differences in learning stage.

(6) Relationship between c-Fos density and behavioral performance.

The study reports that abDGC inhibition increases c-Fos density while impairing performance, whereas mGC inhibition decreases c-Fos density and also impairs performance. This raises an important conceptual question regarding the relationship between overall activity levels and task success. The authors suggest that both sufficient activity and appropriate spatial patterning are required, but the manuscript would benefit from a more explicit discussion of how different perturbations may shift the identity, composition, or coordination of the active neuronal ensemble rather than simply altering total activity levels.

We agree that our findings highlight that successful performance is not determined solely by the overall level of dentate gyrus activity, but rather by the composition and spatial organization of the active neuronal ensemble. In our study, inhibition of abDGCs increased overall mGC activity while disrupting the spatially organized, blade-biased activation pattern and impaired performance. In contrast, direct inhibition of mGCs reduced global excitability but preserved the relative spatial organization of active neurons in animals that continued to perform the task. These findings suggest that different perturbations alter task performance by shifting the identity and coordination of the active neuronal ensemble, rather than simply increasing or decreasing total activity levels. We have now expanded the Discussion to more explicitly address how dentate gyrus computations may depend on the structured recruitment of granule cell ensembles and how distinct manipulations differentially disrupt this organization.

Reviewer #3 (Public review):

Summary:

The authors used genetic models and immunohistochemistry to identify how training in a spatial discrimination working memory task influences activity in the dentate gyrus subregion of the hippocampus. Finding that more cognitively challenging variants of the task evoked more and distinct patterns of activity, they then investigated whether newborn neurons in particular were important for learning this task and regulating the spatial activity patterns.

Strengths:

The focus on precise anatomical locations of activity is relatively novel and potentially important, given that little is known about how DG subregions contribute to behavior. The authors also use a task that is known to depend on this memory-related part of the brain.

Weaknesses:

Statistical rigor is insufficient. Many statistical results are not stated, inappropriate tests are used, and sample sizes differ across experiments (which appear to potentially underlie null results). The chemogenetic approach to inhibit adult-born neurons also does not appear to be targeting these neurons, as judged by their location in the DG.

Please refer to the updated statistical analyses in response to the recommendations below.

Recommendations for the authors:

Reviewing Editor Comments

Please note that reviewers agreed that appropriate revisions are needed to increase the strength of evidence for the paper's claims. Concerns were raised about a lack of statistical rigor in the statistical analyses used. Results of statistical tests were not consistently provided (i.e., statistic applied, value of statistic, degrees of freedom, p-value), and seemingly inappropriate statistical tests were used in some instances. Also, some comparisons had lower statistical power than others. When clarifying the statistical approaches used in the manuscript, we also encourage you to consider reading this article that outlines common statistical mistakes (Makin TR, Orban de Xivry JJ. Ten common statistical mistakes to watch out for when writing or reviewing a manuscript. Elife. 2019 Oct 9;8:e48175. doi: 10.7554/eLife.48175.), such as the importance of not basing conclusions on a significant p-value for one pair-wise comparison vs a non-significant p-value for another pairwise comparison (i.e., groups that are being compared should be included in the same statistical analysis, and interaction effects should be reported when appropriate). We hope that you find this information to be helpful should you decide to submit a revised manuscript to eLife.

Reviewer #1 (Recommendations for the authors):

(1) Standardize TRAP+ quantification across Figure 1.

Please report TRAP+ cell numbers using consistent metrics (e.g., density or percentage) to enable comparison across cell types. In addition, extend the TRAP+ reactivation analysis in Figure 1H to include abDGCs so that reactivation dynamics can be compared directly between mGCs and abDGCs.

Reply in Public Review

(2) Clarify whether dorsal or ventral DG was analyzed in Figure 2.

The differing anatomical distributions of TRAP+ cells under low- and high-demand conditions raise important questions about DG axis specificity. Please indicate whether analyses were performed in dorsal DG, ventral DG, or both, and provide data or justification accordingly.

Reply in Public Review

(3) Acknowledge limitations of the tamoxifen-chow labeling strategy in AsclCreER; hM4 experiments.

Since tamoxifen chow administered over 4-7 weeks labels a heterogeneous abDGC population spanning a broad age range, this approach does not generate birth-dated cohorts. This limitation should be clearly addressed in the text and interpretations, particularly related to cell age-dependent effects, should be tempered.

Reply in Public Review

(4) Revise DREADD quantification using HA rather than mCitrine.

The hM4 mouse line requires HA immunostaining to accurately identify Ascl-lineage cells expressing the DREADD receptor. Because mCitrine is not specific to adult-born neurons and does not reliably reflect hM4 expression, quantification based on mCitrine should be revised.

Reply in Public Review

(5) Include markers to assess abDGC maturation state.

Adding quantification of DCX and NeuN would help define the developmental stage of abDGCs in key experiments and improve the interpretation of cell-age-dependent effects.

Reply in Public Review

(6) Clarify DG layer boundaries and terminology in Figure 2.

If the metric labeled "Distance from the hilus" corresponds to the subgranular zone (SGZ), using SGZ terminology would prevent confusion. Additionally, please provide clearer delineation of DG and hilus borders in sample images.

Reply in Public Review

(7) Provide missing cell number data for Figures 2B and 2C.

Reply in Public Review

(8) Clarify the tamoxifen administration protocol in Figure 6.

Please describe how the protocol selectively targets 6-7-week-old abDGCs and how it differs from the chow-based approach. This will help readers understand the intended specificity of the manipulation.

Reply in Public Review

Reviewer #2 (Recommendations for the authors):

(1) EdU birth-dating timeline

The manuscript would benefit from a clearer description of the EdU birth-dating timeline, ideally with a schematic similar to that provided for BrdU in Supplementary Figure 1.

We appreciate the suggestion. However, we did not include a separate schematic for EdU because its use and birth-dating logic are identical to BrdU (both are thymidine analogs administered systemically and incorporated during S-phase). Therefore, the timeline shown in Supplementary Figure 1 applies equally to both markers. We have clarified this point in the Methods section to avoid confusion.

(2) Clarity of TUNL task description.

The description of the TUNL task, particularly for readers unfamiliar with touchscreen-based paradigms, is difficult to follow without consulting prior literature. A simplified schematic or a clearer step-by-step explanation in the main text or supplementary material would improve accessibility.

We note that the main steps of the TUNL protocol are illustrated in Figure 1A, Supplementary Figure 2A and 2B. Nevertheless, we agree that the description in the text can be made clearer for readers less familiar with touchscreen-based tasks. Thus , we have now revised the Methods section to provide a clearer step-by-step description of the TUNL.

(3) Influence of outliers in Figure 1G.

In Figure 1G, the reported trend that ~1% of 25-39-day-old abDGCs are TRAP+ during LS trials appears to be driven by a small number of outliers. This should be acknowledged, and the wording of the conclusion moderated to reflect the variability in the data.

We agree with the reviewer that the apparent outliers reflect the inherent sparsity of TRAP labeling in this population. In absolute terms, this corresponds to between 0 and 2 TRAP⁺ 25–39-day-old abDGCs per mouse, such that the presence or absence of a small number of labeled cells can appear as outliers when expressed as a percentage. We have revised the text to acknowledge this (see Results).

(4) Presentation of learning curves.

Rather than focusing primarily on "days before criterion" (DBC), it would be helpful to show full learning curves across the entire training period. This would provide a clearer picture of acquisition dynamics and inter-animal variability.

We agree that learning curves can be informative in many behavioral paradigms. However, in our protocol, mice do not undergo the same number of training days because training stops individually once each animal reaches criterion. As a result, plotting full learning curves would produce trajectories of different lengths, making group comparisons difficult and visually cluttered. For this reason, we aligned animals based on days before criterion (DBC), which allows direct comparison of learning dynamics relative to task acquisition. We also consider the cumulative probability representation to be the most appropriate way to summarize learning progression across animals in this context which are also included in the figures.

(5) Clarification of Figure 3B labeling

In Figure 3B, the identity of the orange-labeled group above the LS condition is unclear. Clarification in the figure legend would improve interoperability.

Figure 3B includes two experimental groups. One group performed both the large- and small-separation conditions; this group is shown in orange and labeled LS. Within this group, the upper orange trace corresponds to performance in the large-separation condition, while the lower orange trace corresponds to performance in the small-separation condition. The second group is a control group that performed only the large-separation configuration, and therefore only a single green trace is shown. We agree that this distinction was not sufficiently clear and have revised the figure legend and text to clarify the identity of each trace.

Reviewer #3 (Recommendations for the authors):

(1) Please label figures and, even better, put the legends on the same page.

(2) Just to confirm, in establishing the task, mice performed above 70% for the small separation trials in one of the sessions on 2 consecutive days, for each criterion? Performance seems to be below 70%.

Yes. To meet the criterion, each mouse had to reach ≥70% correct performance in at least one of the two daily sessions on two consecutive days. We then averaged the performance across both sessions for each of those days. As a result, if one session was ≥70% but the other was lower, the daily average could fall below 70%. The values shown in the figure correspond to these daily averages, further averaged across mice.

(3) mGC needs to be explicitly defined. Am I assuming any non-birthdated GC is an mGC according to the authors? (which means it is unknown whether they are in fact mature, though likely most of them are).

In this study, “mature granule cells” (mGCs) refer operationally to granule cells that are not birth-dated with BrdU or EdU and therefore are not classified as adult-born neurons within the defined labeling window. We agree that this population is not directly age-defined, and that while the majority are expected to be mature based on their birth timing relative to the labeling period, we cannot exclude the possibility that a small fraction may include younger, unlabeled neurons. We have now explicitly defined this usage of mGCs in the Methods and clarified this point in the text to avoid ambiguity.

(4) Methods state that Kruskal-Wallis tests were used when more than 3 groups were compared, but I don't see these stats presented (e.g., for trap data in Figure 1, blade x task TRAP expt in Figure 3 (should be 2-way RM anova here and elsewhere), etc) or any corrections for multiple comparisons. I appreciate that the mean rates of TRAPed abGCs are higher in the S and LS groups than in the shaping group, but most mice do not have any BrdU+ cells that are also TRAPed, and there are no statistics here to support the claim. I don't think there is enough sampling to accurately quantify activation of abGCs. Also, no stats to support the claim that TRAPing increases at the "tip of the SB after the more demanding LS task".

We agree with this comment. We have now systematically tested all datasets for normality (by group) and applied parametric tests when the data met normality assumptions, and non-parametric tests otherwise. The statistical analyses have been revised accordingly. We added the appropriate tests (including two-way ANOVA where relevant, such as for blade × group comparisons) and now report full statistics in the figure legends and results sections. For the TRAP analyses in adult-born DGCs, we explicitly acknowledge the very low number of BrdU⁺/TRAP⁺ cells, which limits statistical power and, in some cases, precludes robust statistical testing. These limitations are now clearly stated in the Results and Discussion, and the corresponding interpretations have been tempered. For all Kruskal–Wallis tests, post hoc pairwise comparisons were performed using Dunn’s test, with Bonferroni correction for multiple comparisons, as now specified in the Methods section. We also expanded the Methods to describe the statistical workflow in detail. In addition, we have added the previously missing statistical analysis for Figure 2C. Comparisons were performed between the 0–50% and 50–100% portions of the blade, where 0% corresponds to the apex and 100% corresponds to the distal tip of the blade.

(5) Figure 3I: I can't figure out which effect is statistically significant here (what does the asterisk signify?). Why no individual data points in this graph?

We agree that the absence of individual data points reduced interpretability, and we have now updated the figure to include individual data points to better illustrate data distribution and variability.

(6) The gradient of activity (shap < S < LS) could be due to how long they've been trained on a given stage (e.g. less activity during shaping because they have habituated, and neurons encoding that task phase have already been selected)

We agree that task duration and habituation could, in principle, influence activity levels. Under this interpretation, higher activity would primarily reflect task novelty rather than cognitive demand. However, our data do not support this explanation. Specifically, we found no correlation between the number of training days required to reach criterion and c-Fos–positive or TRAP-positive cell density within a given stage. Thus, animals that reached criterion rapidly did not show higher activity levels than animals that required more days of training and were presumably more habituated to the task demands. This suggests that the observed activity gradient (shaping < S < LS) is not driven by exposure duration or habituation, but rather reflects differences in cognitive demand across task stages.

(7) The TRAP+ EDU+ cell in Figure 3 looks odd because the BrdU signal is (a lot) larger than the TRAP signal, but BrdU is in the nucleus and should be smaller.

We agree that the example in Figure 3 is not optimal. In dividing cells, BrdU/EdU signals can sometimes appear broader or closely apposed, which may affect their apparent size.

(8) For the Ascl-HM4Di experiment, HM4Di appears to be expressed in all of the areas of the granule cell layer where abGCs are NOT located (i.e. no expression in the deep cell layer, near the sgz). This is problematic because it suggests perhaps abGCs are not inhibited as expected.

As noted in our response to Reviewer #1, we did not use the mCitrine to localize the DREADD receptor as it has been demonstrated that mCitrine expression is expressed in a Cre-independent manner and not correlated with hM4Di expression. In the revised manuscript we include a representative image were we performed immunostaining using an HA antibody to directly visualize hM4Di and confirm its expression in adult-born granule cells (Figure 5).

(9) Line 267: "6-7 week old neurons by themselves do not influence either the performance of mice in the task". I don't think this is fair because this experiment wasn't designed with as much power to detect an effect. The group trends are in the same direction, but there are many fewer mice in this experiment (n=6/group) than in the =<7w experiment (n=11/group), where the effect just reached statistical significance.

We are sorry for this confusion which came from an incorrect version. The experiment shown in Figure 6 does not target 6–7-week-old neurons specifically. It uses the same tamoxifen chow–based protocol as Figure 5, but with a shorter exposure (4 weeks vs. 7 weeks), thereby labeling a younger and more restricted cohort of adult-born DGCs. By contrast, Figure 4 targets a more mature population, consisting predominantly of ~5-week-old adult-born neurons as well as mature granule cells (Dock10+).

We have corrected the paragraph accordingly and clarified the age range of the labeled populations in the revised manuscript.

Author Response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

Summary:

Here Bansal et al., present a study on the fundamental blood and nectar feeding behaviors of the critical disease vector, Anopheles stephensi. The study encompasses not just the fundamental changes in blood feeding behaviors of the crucially understudied vector, but then use a transcriptomic approach to identify candidate neuromodulation path ways which influence blood feeding behavior in this mosquito species. The authors then provide evidence through RNAi knockdown of candidate pathways that the neuromodulators sNPF and Rya modulate feeding either via their physiological activity in the brain alone or through joint physiological activity along the brain-gut axis (but critically not the gut alone). Overall, I found this study to be built on tractable, well-designed behavioral experiments.

Their study begins with a well-structured experiment to assess how the feeding behaviors of A. stephensi changes over the course of its life history and in response to its age, mating and oviposition status. The authors are careful and validate their experimental paradigm in the more well-studied Ae. aegypti, and are able to recapitulate the results of prior studies which show that mating is pre-requisite for blood feeding behaviors in Ae. aegypt. Here they find A. stephensi like another Anopheline mosquitoes has a more nuanced regulation of its blood and nectar feeding behaviors.

The authors then go on to show in a Y- maze olfactometer that to some degree, changes in blood feeding status depend on behavioral modulation to host-cues, and this is not likely to be a simple change to the biting behaviors alone. I was especially struck by the swap in valence of the host-cues for the blood-fed and mated individuals which had not yet oviposited. This indicates that there is a change in behavior that is not simply desensitization to host-cues while navigating in flight, but something much more exciting happening.

The authors then use a transcriptomic approach to identify candidate genes in the blood feeding stages of the mosquito's life cycle to identify a list of 9 candidates which have a role in regulating the host-seeking status of A. stephensi. Then through investigations of gene knockdown of candidates they identify the dual action of RYa and sNPF and candidate neuromodulators of host-seeking in this species. Overrall, I found the experiments to be welldesigned. I found the molecular approach to be sound. While I do not think the molecular approach is necessarily an all-encompassing mechanism identification (owing mostly to the fact that genetic resources are not yet available in A. stephensi as they are in other dipteran models), I think it sets up a rich lines of research questions for the neurobiology of mosquito behavioral plasticity and comparative evolution of neuromodulator action.

Strengths:

I am especially impressed by the authors' attention to small details in the course of this article. As I read and evaluated this article I continued to think how many crucial details I may have missed if I were the scientist conducting these experiments. That attention to detail paid off in spades and allowed the authors to carefully tease apart molecular candidates of blood-seeking stages. The authors top down approach to identifying RYamide and sNPF starting from first principles behavioral experiments is especially comprehensive. The results from both the behavioral and molecular target studies will have broad implications for the vectorial capacity of this species and comparative evolution of neural circuit modulation.

I believe the authors have adequately addressed all of my concerns; however, I think an accompanying figure to match the explained methods of the tissue-specific knockdown would help readers. The methods are now explicitly written for the timing and concentrations required to achieve tissue-specific knockdown, but seeing the data as a supplement would be especially reassuring given the critical nature of tissue-specific knockdown to the final interpretations of this paper.

We thank the reviewer for the suggestion and have now incorporated a schematic in the supplementary figure S9B, explaining our methodology for achieving tissue-specific knockdowns.

Reviewer #2 (Public review):

Summary:

In this manuscript, Bansal et al examine and characterize feeding behaviour in Anopheles stephensi mosquitoes. While sharing some similarities to the well-studied Aedes aegypti mosquito, the authors demonstrate that mated-females, but not unmated (virgin) females, exhibit suppression in their blood-feeding behaviour. Using brain transcriptomic analysis comparing sugar fed, blood fed and starved mosquitoes, several candidate genes potentially responsible for influencing blood-feeding behaviour were identified, including two neuropeptides (short NPF and RYamide) that are known to modulate feeding behaviour in other mosquito species. Using molecular tools including in situ hybridization, the authors map the distribution of cells producing these neuropeptides in the nervous system and in the gut. Further, by implementing systemic RNA interference (RNAi), the study suggests that both neuropeptides appear to promote blood-feeding (but do not impact sugar feeding) although the impact was observed only after both neuropeptide genes underwent knockdown.

While the authors have addressed most of the concerns of the original manuscript, a few issues remain. Particularly, the following two points:

(5) Figure 4

The authors state that there is more efficient knockdown in the head of unfed females; however, this is not accurate since they only get knockdown in unfed animals, and no evidence of any knockdown in fed animals (panel D). This point should be revised in the results test as well.

Perhaps we do not understand the reviewer's point or there has been a misunderstanding. In Figure 4D, we show that while there is more robust gene knockdown in unfed females, bloodfed females also showed modest but measurable knockdowns ranging from 5-40% for RYamide and 2-21% for sNPF.

NEW-

In both the dsRNA treatments where animals were fed, neither was significantly different from control. Therefore, there is no change, and indeed this is confirmed by the author's labelling of the figure stats in panel 4D.

We agree with the reviewer and thank them for pointing it out. We have now revised the figure legend and the text to reflect these results (see lines 351-354).

In addition, do the uninjected and dsGFP-injected relative mRNA expression data reflect combined RYa and sNPF levels? Why is there no variation in these data,...

In these qPCRs, we calculated relative mRNA expression using the delta-delta Ct method (see line 975). For each neuropeptide its respective control was used. For simplicity, we combined the RYa and sNPF control data into a single representation. The value of this control is invariant because this method sets the control baseline to a value of 1.

NEW-

The authors are claiming that there is no variation between individual qPCR experiments (particularly in their controls)? Normally, one uses a known standard value (or calibrator) across multiple experiments/plates so that variation across biological replicates can be assessed. This has an impact on statistical analyses since there is no variation in the control data. Indeed, this impacts all figures/datasets in the manuscript where qPCR data is presented. All the controls have zero variation!

We are truly thankful to this reviewer for insisting on this point. It has made us revisit what we thought we understood and now realise were doing wrong (though many in literature do it this way!). We were – incorrectly – setting each control to 1 and calculating relative fold changes for each replicate independently. While this is often seen in literature, we now realise that it is incorrect. We have revisited all our analyses and normalized all samples to the mean ΔCt of the control group, which captures biological variation in both control and experimental groups. All data are now re-plotted to show individual data points for both control and experimental groups, and the error bars on controls represent the biological variation across replicates (Figure 4D, 4F, 4G, S8, S9). Statistical analyses were also revised accordingly, and, importantly, they do not change any conclusions. Please note that the abdominal expression of sNPF and RYa are so low that the controls show very variable baseline expression values.

Reviewer #3 (Public review):

Summary:

This manuscript investigates the regulation of host-seeking behavior in Anopheles stephensi females across different life stages and mating states. Through transcriptomic profiling, the authors identify differential gene expression between "blood-hungry" and "blood-sated" states. Two neuropeptides, sNPF and RYamide, are highlighted as potential mediators of host-seeking behavior. RNAi knockdown of these peptides alters host-seeking activity, and their expression is anatomically mapped in the mosquito brain (sNPF and RYamide) and midgut (sNPF only).

Strengths:

(1) The study addresses an important question in mosquito biology, with relevance to vector control and disease transmission.

Transcriptomic profiling is used to uncover gene expression changes linked to behavioral states.

(2) The identification of sNPF and RYamide as candidate regulators provides a clear focus for downstream mechanistic work.

(3) RNAi experiments demonstrate that these neuropeptides are necessary for normal hostseeking behavior.

(4) Anatomical localization of neuropeptide expression adds depth to the functional findings.

Weaknesses:

(1) The title implies that the neuropeptides promote host-seeking, but sufficiency is not demonstrated and some conclusions appear premature based on the current data. The support for this conclusion would be strengthened with functional validation using peptide injection or genetic manipulation.

(2) The identification of candidate receptors is promising, but the manuscript would be significantly strengthened by testing whether receptor knockdowns phenocopy peptide knockdowns. Without this, it is difficult to conclude that the identified receptors mediate the behavioral effects.

(3) Some important caveats, such as variation in knockdown efficiency and the possibility of offtarget effects, are not adequately discussed.

These comments were addressed in the previous round.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Awesome paper everyone. A delight to read and review.

Thank you very much! We appreciated your comments too!

Reviewer #1 (Public review):

Summary:

This paper examines plasticity in early cortical (V1-V3) areas in an impressively large number of rod monochromats (individuals with achromatopia). The paper examines three things:

(1) Cortical thickness. It is now well established that early complete blindness leads to increases in cortical thickness. This paper shows increased thickness confined to the foveal projection zone within achromats. This paper replicates work by Molz (2022) and Lowndes (2021), but the detailed mapping of cortical thickness as a function of eccentricity and the inclusion of higher retinotopic areas is particularly elegant.

(2) Failure to show largescale reorganization of early visual areas using retinotopic mapping. This is a replication of a very recent study of Molz et al. but I believe, given anatomical variability, the larger n in this study, and how susceptible pRF findings are to small changes in procedure, this replication is also of interest.

(3) Connective field modelling, examining the connections between V3-V1. The paper finds changes in the pattern of connections, and smaller connective fields in individuals with achromatopsia than normally sighted controls, and suggests that these reflect compensatory plasticity, with V3 compensating for the lower resolution V1 signal in individuals with achromatopsia.

This is a carefully done study (both in terms of data collection and analysis) that is an impressive amount of work.

*Effects of eye-movements

The authors have carried out the eye-movement analyses I asked of them. Unfortunately, in 4 individuals they couldn't calibrate the eyetracker (it's impressive they managed in 10). I think this means that 4 of 13 (since a different participant was excluded from head motion) individuals weren't included in correlation analyses. Limiting the correlation analysis to individuals with better fixation has obvious issues. I'd recommend redoing (or additionally including) stats using non-parametric measures while classifying these 4 as having fixation instability of 3 (i.e. greater instability than the participant with the worst fixation who was successfully calibrated).

*Interpreting pRFs

The paper would be strengthened by a little more explicit clarity about what pRFs represent and how that affects their interpretation of their findings as plasticity vs. non-plasticity (I know the authors are aware of this, but I think it would be helpful for readers who are less experienced in pRFs). In the introduction it would be helpful to point out that pRFs represent the collective response of a large population of neurons, and as a result pRF estimates can vary depending on which population of neurons that stimulus drives.

For example, imagine for the sake of argument that rods only project to V1 neurons with larger receptive fields. If one measured pRFs in a control observer under phototopic vs. scotopic conditions one would see smaller pRFs in the photopic conditions. This wouldn't represent 'plasticity' - it would represent the fact that the firing neurons contributing to the pRF signal are a slightly different population because of a change in the stimulus content. This is of course exactly what you see in 2C. And indeed, the authors make this identical point ". In the non-selective condition, the smaller pRFs in controls are in line with the higher spatial resolution of the<br /> cone system, which is not active in the achromat group." But this point would be clearer if more of the conceptual underpinnings were made explicit in the introduction (or at this point in the paper).

Shifts in which population of neurons drive your pRFs can explain main of the more puzzling results in the paper without detracting from your main conclusions. For example, in 2D, I don't think it's differences in S/N driving your results (pRFs are at least theoretically meant to be robust to S/N). If smaller RFs 'drop out' under low luminance and these smaller RFs also tend to be more central, then one would expect the control results of 1D. And I think a similar argument might even be made for the smaller difference in the rod monochromats.

It would be possible to make the point of Figure 4B more simply if Figure 4B was replaced by additional Panels in Figure 2 simply showing V3 pRF sizes/eccentricity distributions. That would make the point that you don't see the same expansion in pRF sizes in V3 in a way that is just as clear, and is closer to the data.

*Interpreting cRFs

Similarly, I think the paper would be improved with more clarity about the underlying signal in CF modeling. Once again, I appreciate that the authors are familiar with this, but it will help the reader in interpretation. (And I do believe thinking carefully about this may alter your interpretations). CF receptive fields 'find' the region in V1 that best predict the V3 signal in a given voxel. In resting state this likely represents a combination of:

(1) visually driven signal - correlations that may or may not reflect connectivity but represent the fact that regions that represent the same region of visual space will be active at the same time.

(2) global bilaterally symmetrical signal consisting of enhanced correlations between iso-eccentric regions (Raemaekers et al., 2014), which may arise from vasculature that symmetrically stems from the posterior cerebral artery (Tong et al., 2013; Tong and Frederick, 2014).

(3) intrinsic neural fluctuations that are more strongly correlated between connected neurons. These are likely quite weak compared to the other contributions.

I think if you ignore 2, (which is not likely to differ between rod mono and controls) and model 1 and 3, you might well see shifts in CFs towards the boundary of the scotoma - essentially the CF's location will be biased towards the region of V1 that has stronger correlations - which = the region which has a visual signal.

I do find convincing the argument that you don't see the same shift in controls in the rod-selective condition. So I think the results of 4A are fine. But a little more clarity about 'what's under the hood' in CF modeling would be nice.

*Interpreting the relationship between pRFs and cRFs

So there's something here that confuses me. We are all agreed that V3 pRF sizes are similar across RM and control. V1 pRFs are larger in RM. It feels intuitive that smaller CFs would compensate but I can't make it make sense to myself when I think it through. Each pRF represents a combination of receptive field location scatter and bandwidth. You want to argue that eccentricity mapping looks pretty normal, so there's no reason to think increased rf scatter, and I can believe that (though I do think this assumption should be discussed explictly).

So far I think we agree.

But let's think about what drives a CF during visual stimulation ... Specifically lets think about 'the pRF of the CF' (the region of visual space represented by the cluster of voxels in the CF). If pRFs for individual voxels in V1 are big, then the pRF for the CF is also going to be large. But we know that pRFs for V3 are normal size. So, the V3 CF will 'find' a smaller number of voxels in V1, in order to try to find the 'correct sized' CF pRF. Note that this explanation is very similar to yours. But doesn't require ANY 'intrinsic' connectivity. It's really just assuming the whole thing is driven by the visual signal and the CF size is determined by the ratio of the pRF sizes in V3 vs. V1.

One possible solution would be to regress out the visual stimulus and redo this analysis based on the residuals.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

This paper examines plasticity in early cortical (V1-V3) areas in an impressively large number of rod monochromats (individuals with achromatopia). The paper examines three things:

(1) Cortical thickness. It is now well established that early complete blindness leads to increases in cortical thickness. This paper shows increased thickness confined to the foveal projection zone within achromats. This paper replicates the work by Molz (2022) and Lowndes (2021), but the detailed mapping of cortical thickness as a function of eccentricity and the inclusion of higher visual areas is particularly elegant.

(2) Failure to show largescale reorganization of early visual areas using retinotopic mapping. This is a replication of a very recent study by Molz et al. but I believe, given anatomical variability (and the very large n in this study) and how susceptible pRF findings are to small changes in procedure, this replication is also of interest.

(3) Connective field modelling, examining the connections between V3-V1. The paper finds changes in the pattern of connections, and smaller connective fields in individuals with achromatopsia than normally sighted controls, and suggests that these reflect compensatory plasticity, with V3 compensating for the lower resolution V1 signal in individuals with achromatopsia.

Strengths:

This is a carefully done study (both in terms of data collection and analysis) that is an impressive amount of work. I have a number of methodological comments but I hope they will be considered as constructive engagement - this work is highly technical with a large number of factors to consider.

Weaknesses:

(1) Effects of eye-movements

I have some concerns with how the effects of eye-movements are being examined. There are two main reasons the authors give for excluding eye-movements as a factor in their results. Both explanations have limitations.

(a) The first is that R2 values are similar across groups in the foveal confluence. This is fine as far as it goes, but R2 values are going to be low in that region. So this shows that eyemovements don't affect coverage (the number of voxels that generate a reliable pRF), but doesn't show that eye-movements aren't impacting their other measures.

We agree with the reviewer that eye movements could affect pRF measures. We have now also included data for all participants where we were able to obtain eye tracking measures and directly tested this relationship. Relevant results are copied below.

Recap of results: 1) as expected gaze was less stable in achromats than controls, 2) achromats with more stable gaze did not show more activation in the scotoma projections zone, which we might have observed if fixation instability masks signals in this region 3) Gaze instability was not correlated with pRF size and eccentricity across V1 in achromats. We note that the relationship between nystagmus and visual sampling is complex - patients experience a stable image and may sample only during a specific phase of the eye movement. It is therefore not inherently clear if and how nystagmus affects pRF size.

Relevant Manuscript text incorporating these analyses is copied below.

To quantify eye movement, we used the following methods added to the manuscript:

“Fixation stability

Participants’ gaze was tracked throughout all pRF mapping runs. Collecting reliable gaze data from individuals with nystagmus is a challenge because out of the box calibration procedures mostly fail without stable fixation. To account for this, we implemented a post-hoc custom calibration procedure (Tailor et al., 2021). The eye-tracker was first precalibrated on a typically sighted individual. Then, before every other run, we collected gaze data from a 5-point fixation task (at fixation and above, below, left, and right of fixation at 5 eccentricity). This data allowed us to subsequently map the patient's recorded gaze coordinates to their precise locations on the screen. In 10 out of the 14 achromats we acquired reliable enough data to assess fixation stability.

Calibration data processing: We first removed the first 0.5 seconds for each fixation location to allow for fixation to arrive on the target. We then performed (a) blink removal, (b) filtered out time points with eye movement velocity outliers (±2SD), and (c) filtered out any positions >3SDs to the left or right of the mean fixation location, and >1SD above or below. We took the median of the remaining gaze measurements as an approximate fixation estimate. The resulting 5 median fixation locations were used to fit an affine transformation that remapped the recorded gaze positions into screen space. 

Quantifying fixation stability: after applying the transformation of the post-hoc calibration, data was filtered for blinks and extreme velocities (<2SD). For each functional run, fixation instability was measured as the standard deviation of gaze x-positions across 1second windows. Measures were then averaged across the two run repeats.”

We report the resulting new fixation data results as follows:

Results (coverage section):

“Another potential confound in our findings is fixation instability. In pRF mapping, which is usually conducted under photopic (cone-dominant) conditions, unstable fixation can cause a signal drop in the foveal projection zone. As expected due to nystagmus, the achromatopsia group showed higher fixation instability compared to controls (rodselective: t_(9.08)=-3.19, p=0.01; non-selective: t<sub<(9.41)</sub>=-4.88, p<0.001 degrees-offreedom corrected for unequal-variance; see Supplement Figure S2a). However, several lines of evidence suggest this instability cannot fully account for the lack of "filling in" in achromats. First, within the achromat group, we found no correlation between fixation stability and coverage (rod-selective: spearman-r₍₈₎ = -0.36, p=0.31; non-selective spearman-r₍₈₎=0.07,p=0.85); Individuals with more stable, control-like fixation did not show more signal inside the scotoma (see Supplement 2). Second, in adults with achromatopsia, typically with less severe nystagmus (Kohl et al., 1993), two recent studies also found absence of filling in (Anderson et al., 2024; Molz et al., 2023).

So, while we cannot fully exclude nystagmus masking foveal signals in the cortex of some patients, this converging evidence from structural and functional MRI measures across different studies and groups, strongly suggests that the deprived cortex does not substantially ‘fill in’ with peripheral rod inputs in achromatopsia.”

Results (pRF size + eccentricity):

“Larger pRFs indicate that neuronal populations in achromats’ V1 cortex, combine information across larger areas in visual space than in typically sighted controls. This could reflect true neural tuning differences as well as be driven by larger eye movement. However, fixation instability in achromats do not significantly correlate with pRF size in our sample (rod-selective: spearman-r₍₈₎ = -0.41, p=0.24; non-selective spearman-r₍₈₎=0.37,p=0.29)

It has been shown that fitting artefacts around scotoma edges, can give rise to similar outward eccentricity shifts (Binda et al., 2013). However, when accounting for fitting artefacts around the foveal scotoma edge by modelling the rod-free zone during pRF fitting, pRF size and eccentricity differences remain unchanged (see Supplement 3). Finally, we found no significant correlations between gaze stability and the eccentricity shift (rod-selective: spearman-r₍₈₎ = 0.58, p=0.08; non-selective spearman-r₍₈₎=0.09,p=0.8, Supplement 4D)

Together, these analyses reveal subtle differences in how V1 of achromats responds to rod signals outside the foveal zone, which are consistent with results from other studies (Molz et al. 2023, Anderson et al. 2024). While we found no direct evidence that these are being driven by confounding factors such as eye-movements or fitting artefacts, more work is needed to understand the underlying processes that give rise to these shifts.”

The following text has been added to Supplement 2

“As expected, achromats showed significant higher fixation instability compared to controls (as reported in the main text). We found no significant correlation between fixation instability and either coverage, pRF size, eccentricity in achromats. Results of Spearman R correlations in both rod- and non-selective conditions are reported in the figure. We note that the relationship between nystagmus and visual sampling is complex- patients experience a stable image and may sample only during specific eyemovement phases. It is therefore not fully clear if and how nystagmus should give rise to altered pRFs.”

(b) The authors don't see a clear relationship between coverage and fixation stability. This seems to rest on a few ad hoc examples. (What happens if one plots mean fixation deviation vs. coverage (and sets the individuals who could not be calibrated as the highest value of calibrated fixation deviation. Does a relationship then emerge?).

In any case, I wouldn't expect coverage to be particularly susceptible to eye-movements. If a voxel in the cortex entirely projects to the scotoma then it should be robustly silent. The effects of eye-movements will be to distort the size and eccentricity estimates of voxels that are not entirely silent.

There are many places in the paper where eye-movements might be playing an important role. 

Examples include the larger pRF sizes observed in achromats. Are those related to fixation instability?

We thank the reviewer for their comment. As detailed in our previous response, we have now extracted fixation instability data from additional patients and have expanded our discussion of its potential effects throughout the manuscript.

Given that fixation instability is expected to increase pRF size by a fixed amount, that would explain why ratios are close to 1 in V3 (Figure 4).

We agree with the reviewer’s point, that the ratio change on its own is not strong evidence of compensation, this analysis was meant to complement the CF result. The plot in Figure 4 is intended to reconcile the connective field (CF) and pRF results. Its purpose is to illustrate that even though larger pRFs in achromats might seem counterintuitive alongside their smaller V3 CF sizes, the pRF data do not contradict the CF findings but they are in fact consistent with one another. We also agree that there are alternative explanations for the differences in pRF size, such as fixation stability, and we have now added this point to the text.

Results (CF size):

“To understand how this finer cortical sampling in V3 (smaller connective fields) impacts visual processing, we consider its effect on population receptive fields (pRFs). In V1, pRF sizes in achromats were significantly larger than in controls for both stimulus conditions, indicating coarser spatial tuning at the cortical input stage (Figure 4C, left). By selectively sampling from a smaller area of the V1 surface (smaller CFs), V3 can effectively compensate for this coarser input. If so, this process should result in a relative normalisation of pRF size in V3 compared to V1 (Figure 4C, right).

To test this prediction, we plotted the ratio of pRF sizes between achromats and controls, where a value of 1 indicates parity between the groups (Figure 4B). As our compensatory connective field hypothesis predicts, the ratio was closer to 1 in V3 than in V1 across both stimulus conditions, confirming the pRF size difference was significantly reduced at the higher cortical stage. Together this shows converging evidence across the two models (pRF and CF) of hierarchical refinement as a possible compensatory mechanism, where V3's altered connectivity helps to normalize the processing of degraded sensory input from V1.”

Discussion:

“The hierarchical reorganisation observed in V3 is unlikely to be driven by fixation instability. Connective field (CF) estimates are robust to eye movements (Tangtartharakul et al., 2023), because they are anchored to V1 inputs rather than absolute screen position. Considered alone, the pRF results could alternatively be explained by eye movements introducing a fixed size offset that affects smaller V1 pRFs more strongly than those in V3. While we found no evidence for this relationship between pRF size and gaze measures in our patients, we cannot fully rule out the possibility. Nevertheless, the internal consistency between the CF and pRF measures provides a more parsimonious account; that sampling across the hierarchy accounts for coarser tuning at the input stage.”

(2) Topography

The claim of no change in topography is a little confusing given that you do see a change in eccentricity mapping in achromats. 

Either this result is real, in which case there *is* a change in topography, albeit subtle, or it's an artifact. 

Perhaps these results need a little bit of additional scrutiny. 

One reason for concern is that you see different functions relating eccentricity to V1 segments depending on the stimulus. That almost certainly reflects biases in the modelling, not reorganization - the curves of Figure 2D are exactly what Binda et al. predict. 

Another reason for concern is that I'm very surprised that you see so little effect of including/not including the scotoma - the differences seem more like what I'd expect from simply repeating the same code twice. (The quickest sanity check is just to increase the size of the estimated scotoma to be even bigger?).

We thank the reviewer for their comment. We have double-checked our scotoma modelling, confirming its correct implementation. The results of the scotoma modelling are not identical to the full one, just similar (see below).

Previous studies on “artificial scotomas” (such as the one reported by Binda et al.) have shown mixed results. While Binda and colleagues found that modelling artificial scotomas normalised pRF shifts, others found no effect (Haak et al. 2012, Prabhakaran et al. 2020). Notably, the rodfree zone in achromatopsia is considerably smaller (~0.5° radius) than most tested artificial scotomas. Moreover, it is unclear whether scotoma modelling is beneficial in clinical populations as artificial scotomas (screen-based masking) are not equivalent to retinal scotomas from inactive photoreceptors. A recent achromatopsia study (Anderson et al. 2024) also found no change in pRF estimates with scotoma modelling.

In our scotoma analyses, we found meaningful differences only in the non-selective condition in controls where cones in the rod-free zone are stimulated - which would be the main expected effect of this modelling exercise (see below). In all other conditions (rod-selective in controls, both conditions in achromats), only rods are stimulated, we found no difference in coverage, eccentricity or pRF size when modelling the scotoma likely because the foveal signal is weak/absent, and did not contribute much to pRF estimates in the unmasked analyses.

This means we cannot account for the eccentricity shift as an edge effect with this scotoma model – but we remain cautious about interpreting it as real. This is because first, as we mention in the paper, in the non-selective condition, which has a higher signal-to-noise ratio, the eccentricity estimates in achromats match those of the control group's rod system. Second, it is still possible that the observed shift is an artefact of modelling that was not accounted for by the approach of scotoma modelling.

Our claim of "no change in topography" specifically referred to the absence of "filling-in" as measured by cortical coverage - the percentage of activated tissue regardless of fitted parameters. However, to avoid confusing given the eccentricity and pRF size results we now rephrased our claim.

Abstract:

“Cortical input stages (V1) exhibited high stability, with input-deprived cortex showing no retinotopic remapping and exhibiting structural hallmarks of deprivation.”

Results (pRF eccentricity):

“It has been shown that fitting artefacts around scotoma edges, can give rise to similar outward eccentricity shifts (Binda et al., 2013). However, when accounting for fitting artefacts around the foveal scotoma edge by modelling the rod-free zone during pRF fitting, pRF size and eccentricity differences remain unchanged (see Supplement 3). Finally, we found no significant correlations between gaze stability and the eccentricity shift (rod-selective: spearman-r₍₈₎ = 0.58, p=0.08; non-selective spearman-r₍₈₎=0.09,p=0.8, Supplement 4D)

Together, these analyses reveal subtle differences in how V1 of achromats responds to rod signals outside the foveal zone, which are consistent with results from other studies (Molz et al. 2023, Anderson et al. 2024). While we found no direct evidence that these are being driven by confounding factors such as eye movements or fitting artefacts, more work is needed to understand the underlying processes that give rise to these shifts.”

To better illustrate the effect of scotoma modelling text has been added to Supplement 3:

“Studies on artificial scotomas, where part of the visual field is masked, suggest that pRF estimates of eccentricity and size can be biased by fitting scotoma-edge artefacts, and that these can be mitigated by modelling the scotoma in the pRF fitting procedure (e.g., Binda et al. 2013).

We therefore repeated the pRF modelling procedure with the rod-scotoma being modelled as a black oval mask (1.25°x0.9°) over the stimulus aperture model. As expected, a visible difference between the two models is only apparent in the nonselective condition in controls where the cones in the rod-free zone are being stimulated. In all the other conditions (rod-selective in controls, and both stimulation conditions in achromats) only the rods are stimulated, therefore the masked stimulus still matches the retinal activation, and no major differences can be observed. Performing the same statistical tests applied to the full model in the main text yields equivalent results of equivalent coverage in the rod-selective condition, with equivalent coverage across groups(t(47) = 0.78, p=0.43, BF10=0.31) and controls show a higher coverage in the non-selective stimulation condition compared to achromats (Mann U(52)=141, p<0.01; unequal variance, reverted to non-parametric).

This consistency in pRF properties when modelling the rod scotoma, is in line with previous results from scotoma modelling; While Binda and colleagues found that this normalised pRF shifts, others found no effect (Haak et al. 2012, Prabhakaran et al. 2020). Notably, the rod-free zone in achromatopsia is considerably smaller (~0.5° radius) than most tested artificial scotomas, and as artificial scotomas (screen-based masking) are not equivalent to retinal scotomas from inactive photoreceptors, it is unclear how artificial scotoma findings generalise to clinical populations. Our results are in line with a recent achromatopsia study (Anderson et al. 2024) which also found no change in pRF estimates with scotoma modelling.”

I'd also look at voxels that pass an R2>0.2 threshold for both the non-selective and selective stimulus. Are the pRF sizes the same for both stimuli? Are the eccentricity estimates? If not, that's another clear warning sign.

Comparable results were obtained when using higher R2 thresholds. These results are now included in Supplement 6.

(3) Connective field modelling

Let's imagine a voxel on the edge of the scotoma. It will tend to have a connective field that borders the scotoma, and will be reduced in size (since it will likely exclude the cortical region of V1 that is solely driven by resting state activity). This predicts your rod monochromat data. The interesting question is why this doesn't happen for controls. One possibility is that there is topdown 'predictive' activity that smooths out the border of the scotoma (there's some hint of that in the data), e.g., Masuda and Wandell.

One thing that concerns me is that the smaller connective fields don't make sense intuitively. When there is a visual stimulus, connective fields are predominantly driven by the visual signal. In achromats, there is a large swath of cortex (between 1-2.5 degrees) which shows relatively flat tuning as regards eccentricity. The curves for controls are much steeper, See Figure 2b. This predicts that visually driven connective fields should be larger for achromats. So, what's going on?

The reviewer raises interesting points about the interpretation of our connective field results. The possibility of differential top-down modulation between controls and achromats is intriguing, however it is not supported by the data, if top-down modulation is activating foveal V1 in controls then we shouldn’t see a drop in the amount of significant vertices sampling from the fovea in the rod-selective condition compared to the non-selective, but in fact we do see quite a large drop in the amount of significant vertices in that area in the rod-selective condition. Therefore, at the moment we do not think there is strong basis to assume our data could be explained by achromats lacking top-down predictive activity in the scotoma area that is present in controls.

Regarding the concern about smaller CFs seeming counterintuitive given the flat eccentricity tuning in achromats' V1: we believe there is not a straightforward prediction from pRF properties to CF sizes. The relationship between V1 pRF characteristics and V3 CF sampling is complex and not well-established in the literature, and the two can be decoupled to some degree. For instance, in our data, controls show flat V1 pRF sizes in the rod-selective condition (similar to achromats), yet their V3 CF sizes maintain the typical eccentricity-dependent increase seen in the non-selective condition. This suggests that CF size patterns don't simply mirror V1 pRF properties or visual stimuli responses.

Importantly, CF modelling fundamentally differs from pRF analysis in how it might be affected by scotomas. Unlike pRF analysis where a scotoma creates a "silent" region in visual space, in CF modelling the deprived cortex remains physically present and continues generating neural signals (albeit not visually-driven ones). If V3-V1 connectivity were anatomically fixed, V3 would continue sampling from deprived V1 regions even if they do not produce visual-driven signals. A change in this sampling pattern, as we see in our data, is therefore evidence for plasticity.

Our data support this interpretation. First, in achromats, the CF size pattern observed cannot be easily explained by scotoma-edge artefacts. V3 vertices sampling from the immediate vicinity of the scotoma (1°-3°) show CF sizes comparable to controls. The effect is only significant further away from the scotoma (4°-6°).

Second, to assess how the presence of a scotoma affects CF measure we can compare the two conditions in the controls, since the rod-selective condition has a scotoma present and the nonselective condition does not. For this purpose, we performed an additional analysis, quantifying on a vertex-by-vertex level the differences in CF fitted parameters between the two stimulation conditions across V1. See results below. In achromats there are no systematic shifts between the stimulation conditions, as expected as both are rod-driven. In controls, this analysis reveals only subtle shifts (~0.45° in the rod-selective condition). CF size has also changed slightly although not significantly different from that observed in achromats. These shifts are much smaller than the CF size and eccentricity differences between controls and achromats, so we consider it unlikely that our findings are driven by scotoma artefacts.

Author response image 1.

Results (CF size):

“The significant CF size differences are unlikely to be a model-fitting bias around a scotoma edge, as V3 vertices sampling from the immediate vicinity of the scotoma (1°3°) show CF sizes comparable to controls. The significant reduction in CF size occurs only further in the periphery (4°-6°), in regions that are primarily stimulus-driven.

To understand how this finer cortical sampling in V3 (smaller connective fields) impacts visual processing, we consider its effect on population receptive fields (pRFs). In V1, pRF sizes in achromats were significantly larger than in controls for both stimulus conditions, indicating coarser spatial tuning at the cortical input stage (Figure 4C, left). By selectively sampling from a smaller area of the V1 surface (smaller CFs), V3 can effectively compensate for this coarser input. If so, this process should result in a relative normalisation of pRF size in V3 compared to V1 (Figure 4C, right).

To test this prediction, we plotted the ratio of pRF sizes between achromats and controls, where a value of 1 indicates parity between the groups (Figure 4B). As our compensatory connective field hypothesis predicts, the ratio was closer to 1 in V3 than in V1 across both stimulus conditions, confirming the pRF size difference was significantly reduced at the higher cortical stage. Together this shows converging evidence across the two models (pRF and CF) of hierarchical refinement as a possible compensatory mechanism, where V3's altered connectivity helps to normalize the processing of degraded sensory input from V1.”

Discussion (added paragraph):

“The hierarchical reorganisation observed in V3 is unlikely to be driven by fixation instability. Connective field (CF) estimates are robust to eye movements (Tangtartharakul et al., 2023), because they are anchored to V1 inputs rather than absolute screen position. Considered alone, the pRF results could alternatively be explained by eye movements introducing a fixed size offset that affects smaller V1 pRFs more strongly than those in V3. While we found no evidence for this relationship between pRF size and gaze measures in our patients, we cannot fully rule out the possibility. Nevertheless, the internal consistency between the CF and pRF measures provides a more parsimonious account; that sampling across the hierarchy accounts for coarser tuning at the input stage.”

The beta parameter is not described (and I believe it can alter connective field sizes).

In Author response image 2, we plot the beta parameter of the pRF modelling in V1 with no R² filtering, error bars are 95% CIs:

Author response image 2.

The reviewer did not specify how beta might alter connective field sizes. We assume he meant that as in pRF mapping, the slope of activity from deprived to non-deprived cortex will artefactually create a CF model fit with smaller CF sizes. To test this, we calculated the slope of beta values between 0° and 3° in each participant in the rod-selective condition, as this range includes the scotoma and the area at the edge of the scotoma. We then used the slope as a covariate in an ANCOVA when comparing the CF sizes across groups in each sampled V1 segment. Accounting for the beta slope of V1 did not change the reported results. This analysis still shows smaller CF sizes in V3 in the rod-selective conditions between 4°-6° eccentricity – these differences remain significant (p<0.001 for 4°-5° and p<0.05 for 5°-6° when comparing achromats vs controls).

Similarly, it's possible to get very small connective fields, but there wasn't a minimum size described in the thresholding.

CF sizes were fit with a grid fit. Possible values were [0.5,1,2,3,4,5,7,10]. Therefore, the minimum size is 0.5. Filtering out the smallest connective field sizes does not change the results:

Author response image 3.

I might be missing something obvious, but I'm just deeply confused as to how the visual maps and the connectome maps can provide contradictory results given that the connectome maps are predominantly determined by the visual signal. Some intuition would be helpful.

We agree that this appears counterintuitive, and now added further clarification. The two models (pRF and CF) fundamentally differ in what they measure and how they relate to visual processing. V1 pRF sizes reflect the relationship between neural activity and visual stimuli - essentially how much of a visual stimulus drives a voxel's response - while V3 CF sizes reflect how V3 samples from the V1 cortical surface, indicating how many V1 voxels contribute to a V3 voxel's activity.

The measures constrain each other, as a V3 voxel's pRF size is expected to match the pooling of its connected V1 inputs. But they can be decoupled: A V3 voxel could sample from a small area of V1 cortex (a small CF in mm) that happens to represent a large area of visual space if those V1 voxels have large pRFs. The aim of Figure 4B is to clarify that the measures are consistent with one another even though they diverge in direction. In achromats, where V1 voxels have larger pRFs (coarser spatial resolution), V3 appears to compensate by sampling more selectively from V1 via smaller CF sizes. Theoretically, this should reduce the pRF size difference between controls and patients in V3, a prediction that our data supports.

Results (CF size):

“To understand how this finer cortical sampling in V3 (smaller connective fields) impacts visual processing, we consider its effect on population receptive fields (pRFs). In V1, pRF sizes in achromats were significantly larger than in controls for both stimulus conditions, indicating coarser spatial tuning at the cortical input stage (Figure 4C, left). By selectively sampling from a smaller area of the V1 surface (smaller CFs), V3 can effectively compensate for this coarser input. If so, this process should result in a relative normalisation of pRF size in V3 compared to V1 (Figure 4C, right).

To test this prediction, we plotted the ratio of pRF sizes between achromats and controls, where a value of 1 indicates parity between the groups (Figure 4B). As our compensatory connective field hypothesis predicts, the ratio was closer to 1 in V3 than in V1 across both stimulus conditions, confirming the pRF size difference was significantly reduced at the higher cortical stage. Together this shows converging evidence across the two models (pRF and CF) of hierarchical refinement as a possible compensatory mechanism, where V3's altered connectivity helps to normalize the processing of degraded sensory input from V1.”

Discussion (added paragraph):

“The hierarchical reorganisation observed in V3 is unlikely to be driven by fixation instability. Connective field (CF) estimates are robust to eye movements (Tangtartharakul et al., 2023), because they are anchored to V1 inputs rather than absolute screen position. Considered alone, the pRF results could alternatively be explained by eye movements introducing a fixed size offset that affects smaller V1 pRFs more strongly than those in V3. While we found no evidence for this relationship between pRF size and gaze measures in our patients, we cannot fully rule out the possibility. Nevertheless, the internal consistency between the CF and pRF measures provides a more parsimonious account; that sampling across the hierarchy accounts for coarser tuning at the input stage.”

Some analyses might also help provide the reader with insight. For example, doing analyses separately on V3 voxels that project entirely to scotoma regions, project entirely to stimulusdriven regions, and V3 voxels that project to 'mixed' regions.

We agree that it is important to plot the connective field dynamics across the scotoma region.

In Figure 4A we split the V3 vertices based on the V1 area they sample from. Therefore the 0°-1° would be considered as mainly sampling from the “scotoma” region and the higher the eccentricity is, the less “scotoma” it includes. The V3 vertices that have a significantly smaller CF size compared to controls are those sampling from mostly if not entirely stimulusdriven regions 4°-5° and 5°-6°. We are not sure how further binning the data by within, across and outside scotoma would be more informative.

However, in Author response image 4, we plot in more details the distribution of CF sizes sampling from a V1 segment clearly inside and clearly outside the scotoma. The top figure shows the CF size distribution of V3 vertices that sample from a V1 0°-1° segment, where V1 is deprived of input due to the rod scotoma. In achromats, there is a clear drop in vertices with a very small (0.5) CF size. The bottom figure shows the distribution of V3 vertices that sample from the V1 4°-5° segment which falls outside the scotoma and shows a significant difference in CF size across the groups. Here in achromats you can see a drop in larger V3 CF sizes sampling from the V1 region, and an increase in smaller ones (note that this further addresses a previous concern that connective field differences across groups are solely driven by very small CFs).

Author response image 4.

Following the reviewer’s comment we have added the following statement in the results section discussing CF size:

“The significant CF size differences are unlikely to be a model-fitting bias around a scotoma edge, as V3 vertices sampling from the immediate vicinity of the scotoma (1°3°) show CF sizes comparable to controls. The significant reduction in CF size occurs only further in the periphery (4°-6°), in regions that are primarily stimulus-driven.”

The finding that pRF sizes are larger in achromats by a constant factor as a function of eccentricity is what differences in eye-movements would predict. It would be worth examining the relationship between pRF sizes and fixation stability.

We found no relationship between fixation stability and pRF size in V1, although as we explain in response to an earlier point, this does not fully exclude the reviewers alterative explanation, which we now add to the discussion.

Discussion:

“The hierarchical reorganisation observed in V3 is unlikely to be driven by fixation instability. Connective field (CF) estimates are robust to eye movements (Tangtartharakul et al., 2023), because they are anchored to V1 inputs rather than absolute screen position. Considered alone, the pRF results could alternatively be explained by eye movements introducing a fixed size offset that affects smaller V1 pRFs more strongly than those in V3. While we found no evidence for this relationship between pRF size and gaze measures in our patients, we cannot fully rule out the possibility. Nevertheless, the internal consistency between the CF and pRF measures provides a more parsimonious account; that sampling across the hierarchy accounts for coarser tuning at the input stage.”

Reviewer #2 (Public review):

Summary:

The authors inspect the stability and compensatory plasticity in the retinotopic mapping in patients with congenital achromatopsia. They report an increased cortical thickness in central (eccentricities 0-2 deg) in V1 and the expansion of this effect to V2 (trend) and V3 in a cohort with an average age of adolescents.

In analyzing the receptive fields, they show that V1 had increased receptive field sizes in achromats, but there were no clear signs of reorganization filling in the rod-free area. In contrast, V3 showed an altered readout of V1 receptive fields. V3 of achromats oversampled the receptive fields bordering the rod-free zone, presumably to compensate and arrive at similar receptive fields as in the controls.

These findings support a retention of peripheral-V1 connectivity, but a reorganization of later hierarchical stages of the visual system to compensate for the loss, highlighting a balance between stability and compensation in different stages of the visual hierarchy.

Strengths:

The experiment is carefully analyzed, and the data convey a clear and interesting message about the capacities of plasticity. 

Weaknesses:

The existence of unstable fixation and nystagmus in the patient group is alluded to, but not quantified or modeled out in the analyses. The authors may want to address this possible confound with a quantitative approach.

We have responded to this in the “Recommendations for the authors” section of this reviewer, as they included a more detailed description of these points there.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) I think the term rod monochromats should be included early in the paper since it's a more intuitive term to describe this population.

We agree with the reviewer that the term “rod monochromats” is more intuitive as it clarifies the retinal source of the disease but have chosen the term achromats for consistency with a wide literature of published work in this group, including our own and our close collaborators’. To clarify, in the first mention of the group as achromats in the introduction we have now added this term:

“Achromatopsia (also known as rod monochromacy) causes cone photoreceptors in the retina to be inactive from birth (Aboshiha et al., 2014).”

(2) The paper essentially contains two definitions of 'eccentricity'. One (atlas/segments) comes from the Benson atlas and the other (functional) comes from pRF mapping. It would be good to make this distinction terminology clearer earlier in the paper. It would also be good to use more consistent terminology. I assume 'sampled atlas V1 eccentricity' in 3A is the same as 'V1 segment' in 1A?

For consistency we have now referred to these as V1 segment and sampled V1 segment in the figures when describing the atlas-based definition, and eccentricity for the measured pRF-based eccentricity.

(3) The 'stability vs. plasticity' framing in the introduction could be tightened slightly.

We have made the following changes following the reviewer’s comment:

“In the visual domain, the focal point of the debate on plasticity and stability has hinged on the extent to which retinal input deprivation can drive local reorganisation in early visual cortex, for example, for deprived tissue to take on inputs from spared retinal locations (Adams et al., 2007; Baker et al., 2005, 2008; Baseler et al., 2002, 2011; Calford et al., 2005; Dilks et al., 2009; Dumoulin & Knapen, 2018; Ferreira et al., 2016; Goesaert et al., 2014; Haak et al., 2015; Molz et al., 2023; Ritter et al., 2019; Schumacher et al., 2008). In reality visual impairment is a more global phenomenon, affecting all levels of visual processing, with complex dynamics beyond constricted local retinocortical projection zones(Carvalho et al., 2019).”

(4) Figure 1A, define the x axis as degrees.

We have now added the ° sign to all the tick labels indicating Benson map eccentricity.

(5) Figure 2B, is there room for pictures of the silent substitution/standard stimulus

We have now added images in a Supplement 5 to avoid cluttering the main Figure 2B

(6) Figure 2

Panel A has a slightly weird organization. The reader is supposed to compare the square symbols to each other, and the circles to each other, why not organize the figure so they are adjacent in the graph (i.e. non selective control, non-selective achromat, selective control, selective achromat)? That also helps the reader orient that in the non-selective conditions you have almost complete pRF coverage. 

We have taken on the reviewer’s suggestion and changed the order.

In the inset, maybe use empty symbols? That's the traditional way to say that the square/circle applies to both red and black.

We prefer the current format.

Figure 2C - the symbols change to circles? Why not keep the symbols of A?

We have now changed the symbols of 2C&D.

I'd put the non-selective maps above the selective maps?

We appreciate the feedback but prefer to keep it as it is, as we feel the critical point is conveyed by the rod maps.

(7) 'We propose a new hierarchical model of neural adaptation'. These ideas are hardly new. There are also other models, that would explain your data (cumulative plasticity) https://www.ncbi.nlm.nih.gov/pmc/articles/PMC5953572/

We thank the reviewer for the reference. We have now cited it in our discussion and removed the word “new” form the mentioned sentence.

“Therefore, there is theoretically broader scope for experience-dependent reweighting of inputs (Beyeler et al., 2017; Makin & Krakauer, 2023) and to optimise use of inputs that are still available, more reliable, or more relevant in the impaired system. Conversely, higher-order visual areas may appear more plastic simply because they integrate the cumulative effects of learning from multiple lower stages (Beyeler et al., 2017).”

We propose a hierarchical model of neural adaptation…” [deleted the word new]

(8) Line 508. No image of the stimulus is contained in the paper

Corrected

(9) Line 620. I believe the Figure is 1B, not 1C.

Corrected

(10) Figure 4A. CF Size - add mm2 to the axes.

Corrected

Reviewer #2 (Recommendations for the authors):

I am not an expert on pRF mapping, and as such, I am unsure how to relate to pRF mapping performed in patients with unstable fixation (not quantified, but referred to) and nystagmus, such as the achromatic population here. Since the majority of the results hinge on this analysis, I would appreciate more data about the differences between the groups. Supplement 2, which is meant to speak to this, shows only the data from 3 typical participants, and in itself is not evidence for "no correlation between stable fixation and enhanced foveal". Additionally, I'd appreciate a clear methods explanation of how the authors address these confounds; this is too important a concern to be left for the discussion section.

We agree with the reviewer that eye movements could affect pRF measures. We have now also included data for all participants where we were able to obtain eye tracking measures and directly tested this relationship. Relevant results are copied below.

Recap of results: 1) as expected gaze was less stable in achromats than controls, 2) achromats with more stable gaze did not show more activation in the scotoma projections zone, which we might have observed if fixation instability masks signals in this region 3) Gaze instability was not correlated with pRF size and eccentricity across V1 in achromats. We note that the relationship between nystagmus and visual sampling is complex - patients experience a stable image and may sample only during a specific phase of the eye movement. It is therefore not inherently clear if and how nystagmus affects pRF size.

Relevant Manuscript text incorporating these analyses is copied below.

To quantify eye movement, we used the following methods added to the manuscript:

“Fixation stability

Participants’ gaze was tracked throughout all pRF mapping runs. Collecting reliable gaze data from individuals with nystagmus is a challenge because out of the box calibration procedures mostly fail without stable fixation. To account for this, we implemented a post-hoc custom calibration procedure (Tailor et al., 2021). The eye-tracker was first precalibrated on a typically sighted individual. Then, before every other run, we collected gaze data from a 5-point fixation task (at fixation and above, below, left, and right of fixation at 5 eccentricity). This data allowed us to subsequently map the patient's recorded gaze coordinates to their precise locations on the screen. In 10 out of the 14 achromats we acquired reliable enough data to assess fixation stability.

Calibration data processing: We first removed the first 0.5 seconds for each fixation location to allow for fixation to arrive on the target. We then performed (a) blink removal, (b) filtered out time points with eye movement velocity outliers (±2SD), and (c) filtered out any positions >3SDs to the left or right of the mean fixation location, and >1SD above or below. We took the median of the remaining gaze measurements as an approximate fixation estimate. The resulting 5 median fixation locations were used to fit an affine transformation that remapped the recorded gaze positions into screen space.

Quantifying fixation stability: after applying the transformation of the post-hoc calibration, data was filtered for blinks and extreme velocities (<2SD). For each functional run, fixation instability was measured as the standard deviation of gaze x-positions across 1second windows. Measures when then averaged across the two run repeats.”

Results (coverage section):

“Another potential confound in our findings is fixation instability. In pRF mapping, which is usually conducted under photopic (cone-dominant) conditions, unstable fixation can cause a signal drop in the foveal projection zone. As expected due to nystagmus, the achromatopsia group showed higher fixation instability compared to controls (rodselective: t_(9.08)=-3.19, p=0.01; non-selective: t<sub<(9.41)</sub>=-4.88, p<0.001 degrees-offreedom corrected for unequal-variance; see Supplement Figure S2a). However, several lines of evidence suggest this instability cannot fully account for the lack of "filling in" in achromats. First, within the achromat group, we found no correlation between fixation stability and coverage (rod-selective: spearman-r₍₈₎ = -0.36, p=0.31; non-selective spearman-r₍₈₎=0.07,p=0.85); Individuals with more stable, control-like fixation did not show more signal inside the scotoma (see Supplement 2). Second, in adults with achromatopsia, typically with less severe nystagmus (Kohl et al., 1993), two recent studies also found absence of filling in (Anderson et al., 2024; Molz et al., 2023).

So, while we cannot fully exclude nystagmus masking foveal signals in the cortex of some patients, this converging evidence from structural and functional MRI measures across different studies and groups, strongly suggests that the deprived cortex does not substantially ‘fill in’ with peripheral rod inputs in achromatopsia.”

Results (pRF size + eccentricity):

“Larger pRFs indicate that neuronal populations in achromats’ V1 cortex, combine information across larger areas in visual space than in typically sighted controls. This could reflect true neural tuning differences as well as be driven by larger eye movement. However, fixation instability in achromats do not significantly correlate with pRF size in our sample (rod-selective: spearman-r₍₈₎ = -0.41, p=0.24; non-selective spearman-r₍₈₎=0.37,p=0.29)

It has been shown that fitting artefacts around scotoma edges, can give rise to similar outward eccentricity shifts (Binda et al., 2013). However, when accounting for fitting artefacts around the foveal scotoma edge by modelling the rod-free zone during pRF fitting, pRF size and eccentricity differences remain unchanged (see Supplement 3). Finally, we found no significant correlations between gaze stability and the eccentricity shift (rod-selective: spearman-r₍₈₎ = 0.58, p=0.08; non-selective spearman-r₍₈₎=0.09,p=0.8, Supplement 4D)

Together, these analyses reveal subtle differences in how V1 of achromats responds to rod signals outside the foveal zone, which are consistent with results from other studies (Molz et al. 2023, Anderson et al. 2024). While we found no direct evidence that these are being driven by confounding factors such as eye-movements or fitting artefacts, more work is needed to understand the underlying processes that give rise to these shifts.”

The following text has been added to Supplement 2

“As expected, achromats showed significant higher fixation instability compared to controls (as reported in the main text). We found no significant correlation between fixation instability and either coverage, pRF size, eccentricity in achromats. Results of Spearman R correlations in both rod- and non-selective conditions are reported in the figure. We note that the relationship between nystagmus and visual sampling is complex- patients experience a stable image and may sample only during specific eyemovement phases. It is therefore not fully clear if and how nystagmus should give rise to altered pRFs.”

The field connectivity analysis similarly seems to be used only on task data from the same design; if it was replicated from resting-state data, that would be a good way to show consistency which is independent of measures requiring fixation. 

We agree that resting-state data would be valuable; however, we did not collect such data in these individuals due to time limitations. Instead, we demonstrate the consistency and reliability of our results by replicating our findings across two different stimulation conditions (rod-selective and non-selective), which differ in luminance, contrast and signal amplitude in both groups and for controls also in the photoreceptors involved. The convergence of results across these distinct visual conditions strengthens our confidence in the reliability of the observed effects. Also, notably, CF estimates have been shown to be robust to large eye movements, and therefore also to differences in fixation stability across groups (Tangtartharakul et al., 2023).

The authors may want to contextualize their findings in relation to what reorganization exists in cases of late-onset loss of part of the visual field on one hand (stroke recovery), and in the case of complete blindness from early life on the other, as both speak to different levels of plasticity the visual system is capable of.

We thank the reviewer for their comment and have added a new paragraph discussing this topic.

Discussion:

“Our findings on hierarchical adaptation have broader implications for other visual disorders, depending on their timing and nature. For instance, a central scotoma acquired in adulthood, as in macular degeneration, may not trigger the same V3 sampling shifts (Haak et al., 2016), suggesting a sensitive window for this form of plasticity, after which connective fields remain more stable. This also raises questions about congenital blindness, where the absence of any driving input could lead to weakening or repurposing of hierarchical connections (Saccone et al., 2024). Moreover, principles may differ between a deprived but structurally intact cortex, as in retinal dystrophies, and a physically damaged cortex, as in stroke. In the latter, more extensive reorganisation may be required to sample effectively from surviving, and potentially disparate, regions of V1. Perceptual training effects in stroke rehabilitation may reflect such dynamics (Cavanaugh et al., 2025; Elshout et al., 2021).”

A more minor point: Can the authors clarify what the dark adaptation is used for, and provide the supplementary analysis showing that the duration difference for some of the participants didn't impact the results (stated but not shown).

The dark adaptation period before the rod-selective condition allowed rod photoreceptors to recover from bleaching caused by prior mesopic light exposure, ensuring optimal rod sensitivity under scotopic conditions. To verify that our 15-minute adaptation period was sufficient, we tested 10 control participants with an extended 45-minute adaptation period. As we found no differences in the resulting rod maps between standard and extended adaptation protocols, these participants were combined with the main control group for all analyses. Author response image 5 are the plots for the two dark adaptation periods.

Author response image 5.

On 2020-05-01 09:48:59, user Kasper Kepp wrote:

This paper on the state-of-the-art Danish blood-donor data finds a IFR = 0.08% for people between 0-69 years of age. The study is very important because the sampling bias from case fatality ratios (the iceberg effect of knowing almost all deaths but only the most symptomatic cases, i.e. missing the dark number) is largely removed.

By interpolation, the Danish population now has approximately 1.6% infection, corresponding to 100,000 people out of 6 million. The dark number stands at 12-fold the known cases (7-18).

Some minor sampling biases remain (people who are blood donors need to be healthy and may be socioeconomically skewed) but considering the wide blood donor representativeness in Denmark, I think all Danish researchers will agree that sampling bias must be small.

The IFR is also fully in line with the most representative data we have from Iceland (14% of population tested, 48000 tests), where the sampling bias is essentially eliminated, which stands at approximately 0.56% (10 deaths / 1799 cases as of May 1) and includes all the high-risk individuals >70 years. https://www.worldometers.in...

Compared to the Santa Clara study, which caried potential major sampling bias, this issue seems to be now largely removed. Consensus in Denmark is now emerging that the overall whole-population crude mortality of covid-19 is of the order of 0.25-0.6%, in excellent agreement with the Iceland data.

These two countries have not have their health care systems strained, making them the relevant data also for this reason for pinpointing the "real" mortality of covid-19 absent overmortality by capacity exhaustion as seen in some other countries.

Obviously, the fact that the IFR is 0.08% for the 0-69 year old has enormous implications for political decision making in Scandinavia, as it evidences that most of the population can build immunity at much reduced mortality than previously assumed.

On 2020-04-22 16:02:39, user Texas Longhorns wrote:

The research paper does not indicate how many of those that participated had already been tested for Covid and what those test results were.

If they over sampled people that had already tested positive and recovered of course you will get a higher rate of positive antibodies. That would not be indicative of the general population.

There is also the problem of false positives because the test can trigger for the common cold that is also a coronavirus.

I don't think this research passes muster as any reliable indication of antibodies in the general population and should absolutely not be used as a basis to reopen businesses and large public gatherings.

Having antibodies to one strain of the virus may not give you any immunity to the more than 8 strains of Covid we know are out there.

Even if the test results are accurate at 2% that is nothing and you need at least 60% solid immunity to consider any large population to have herd immunity protection.

On 2020-04-10 13:51:26, user steve rubin wrote:

Does anyone know peak hospitalization during the 2017-2018 flu season? From the cdc summary there were 808,000 total hospitalizations with 61,000 deaths and I remember the flu season was pretty long. I wonder how the curves for new cases, deaths, hospitalizations and icu use looked. I remember stories that the hospitals were crowded but I don't remember stories about people dying because there weren't beds or ventilators.

I know that it's unpopular to compare coronavirus to the flu. Underestimating a threat is dangerous and could (and maybe did) lead to delay in ramping up testing and beds and ventilators and other necessary medical resources.

When people were predicting 2,000,000 deaths in the US and then 200,000 deaths I could understand the fears. But now they're predicting 60,000 deaths and it may end up half of that, so I think it's reasonable to make the comparisons.

Comparing situations to past situations is usually our best way to understand how to react. In terms of how contagious and how lethal this epidemic/pandemic is, it now seems that it and the flu are similarly contagious and that covid is much less lethal. The big difference is that we have a pretty big number of people with significant immunity to the flu while it's likely there was little immunity in our population to covid-19. If we end up with 200,000,000 people becoming infected but with only 60,000 deaths, then covid was a fifth as lethal as the flu for 2017-2018 with 3 in 10,000 infections dying vs 14 in 10,000 infections dying from the flu.

However the comparison to the flu can lead to some counter-arguments. For example, the cdc uses a multiplier of ~80 for estimated current flu infections vs confirmed flu infections. Applying that to covid-19 means that we have ~500,000 confirmed cases so we would have had 40,000,000 total infections leaving another 160,000,000 to go assuming 60% of the population for herd immunity. Projecting deaths would mean 17,000 + 68,000 for a total of 85,000. We'll soon know what that multiplier is for covid-19 because there are a number of antibody surveys going on in the US and internationally. You can bet that the same thing will happen for the flu next year and we'll have a more accurate estimate of infections and lethality for the flu rather than the current guesstimates.

A big question is how social distancing will have affected the final number of infections and deaths. It seems so logical that social distancing will curb infections and deaths, but many suggest that it may end up only prolonging the length of the pandemic while not making a significant difference in total final infections and total final deaths. The antibody tests may give us the answer to that as well.

On 2020-05-20 17:49:28, user Christopher Leffler wrote:

Bottom line, how many people does Dr. Ioannidis think will die in the US from this epidemic? If one reads the paper, he proposes that " even under congested circumstances, like cruise ships, aircraft carriers or homeless shelter, the proportion of people infected does not get to exceed 20-45%."<br /> Also, he believes that the infection fatality ratio is: " Infection fatality rates ranged from 0.03% to 0.50% and corrected values ranged from 0.02% to 0.40%."<br /> So, these numbers would give estimates for the United States of:<br /> Low end: 331,000,000 people * 0.2 * 0.0002 = 13,240.<br /> High end: 331,000,000 people * 0.45 * 0.004 = 595,800.<br /> The range is so wide as to provide no useful information. And of course, the pandemic is already at 92,387 deaths in the US, as of May 20, 2020. So we know Ioannidis low end is simply wrong.<br /> We have looked at the mortality in different age groups in New York, among residents and transit workers, and on the Diamond Princess:<br /> https://www.medrxiv.org/con...<br /> Quite early in the pandemic (early April), we showed that if the US followed the course that Italy and Spain had already experienced, we would see 100,000 dead in the US:<br /> https://www.researchgate.ne...<br /> More recently, we showed that if the mortality rates seen in New York MTA / New York State / Diamond Princess were observed nationally, the mortality could be over 600,000, which is the high end for Ioannidis work also:<br /> https://www.researchgate.ne...<br /> So, the bottom line is, that the high end projections from all groups could be quite high indeed. So we will need to be vigilant--wearing masks, protecting the vulnerable, etc. The pandemic is real. To say that it is similar to a typical flu is just plain false. Even Ioannidis own projections do not rule out that this is far worse than the flu. When is the last year the flu killed 92,000 Americans and was on track to kill potentially hundreds of thousands more?

On 2020-10-07 12:44:20, user Iratxe Puebla wrote:

Review completed as part of ASAPbio’s #PreprintReviewChallenge

The study examines the incidence of heart disease deaths in the early pandemic period in the US (30 March to April 26) in areas without large COVID-19 outbreaks. The authors sought to study whether a decline in acute myocardial infarction (AMI) admissions was linked to either a higher mortality rate (which would suggest avoidance of care seeking), or lower mortality (which may suggest less triggers for AMI). The authors use data from the CDC’s s National Center for Health Statistics and apply inclusion criteria requiring >97% completeness for the data.

The study includes data from a reliable source and includes controls involving a comparison to incidence of heart disease deaths in the same period in 2019 and 4 weeks earlier in 2020. While the study is observational and can only point to trends and not explain the reported decrease in incidence of heart disease death in several states during the study period, it helps surface this trend and opens lines for further research to evaluate whether the trend will sustain over a longer period and if so, look into the potential factors behind the trend. If the trend were to sustain over time and was found not to be associated with misclassification of death cause, it may provide avenues to identify factors that can reduce triggers for AMI.

Minor comments<br /> - The authors indicate ‘The primary analysis captured 747,375,188 person-weeks for the early pandemic period and 101,620,248 person-weeks for the 2019 control period’ the number of person weeks for the control period is considerably lower, can the authors provide some context for this, and whether this may have any influence on the analysis?<br /> - The abstract indicates ‘The mean incidence rate (per 100,000 person-weeks) for heart disease in states without excess deaths during the early pandemic period was 3.95 (95% CI 3.83 to 4.06) versus 4.19 (95% CI 4.14 to 4.23) during the corresponding period in 2019’, the Results section reads ‘The mean incidence rate (per 100,000 person-weeks) for heart disease in states without excess deaths during the early pandemic period was 3.95 (95% CI 3.83 to 4.06) versus 4.35 (95% CI 4.23 to 4.48)’ it appears they need to be updated to match?

Questions for the authors<br /> - Now that we have data from four additional months into the pandemic, are the authors planning an extension to the analysis?<br /> - For the states where an increase in the incidence of heart disease deaths was observed, the authors mention the possibility of harm due to avoidance of care, misclassification during a period of excess deaths and COVID-19 itself increasing cardiovascular deaths. Do the authors think that capacity at hospitals may have been a factor behind any increase in heart disease deaths? E.g. related to prioritization of COVID-19 admissions vs others.

On 2020-10-26 17:59:08, user Meng-Ju Wu wrote:

Hi! It is interesting to read the paper in discussion for EVs to differentiate ALS from healthy and diseased groups. And I want to share my thought on the study.

I think the main contribution of the study includes the purification of EVs with the nickel-based isolation compared to the conventional methods that makes the analysis of specific EV parameters highly sensitive and reliable. If the EVs are reliably differentiate ALS patients from healthy and diseased group, clinical assessment with the blood test will significantly shorten the diagnosis time for ALS and that the treatment may be started as early as possible. In addition, if biomarkers are available to detect ALS patients, it means that we can develop the treatment specific to ALS using their unique properties. Patients can avoid costly and lengthy process of ALS diagnosis.

I have two questions considering the methods. First, why was the supernatant from human plasma diluted in filtered PBS once but the serum from mice required 10 times for dilution? Second, what was the temperature and humidity condition for the incubation of activated charged agarose beads in NBI? I think the time to use the obtained serum would be the limitation of this approach. The content of the EVs might be changed if the centrifuged plasma samples are not immediately used. Such compositional change may be subject to the storage condition and the degradation rate of each specific proteins. It may also vary among species. Therefore, a specific time period to analyze the plasma should be strictly regulated.

In general, I think there are no major grammatic or spelling errors. However, the content may be modified in order to make it more logical and convincing to read. In the introduction part, I think it is important to summarize how is ALS diagnosed clinically. If the readers are informed that electrophysiologic diagnosis takes longer time and effort and make the diagnosis, they would appreciate the value of blood test to detect suspected ALS patient in prodromal state. In the last paragraph of the introduction, it is not reasonable to mention that the study results suggesting EVs are food biomarkers. It should be mention in the discussion or conclusion section. In the material section, the time of patient inclusion was missing. In the animal model, the paper should mention why only female mice with SOD1G93A and male mice with TDP-43Q331K were studied. Also, the timing to study the two different genes as well as the number of the mice were concerning to interpret the results. I want to suggest making a visual diagram on the machine learning technique. You did a great job in comparing the difference between ultracentrifugation and NBI using EV-like liposomes. As such, I want to suggest applying the same comparison onto the animal model to test the reliability of the using the NBI method alone in the paper. The results and the discussion are well-written and consistent with the tables and figures provided

On 2021-06-23 21:55:50, user David Wiseman PhD wrote:

Summary:<br /> Regarding the continued and unnecessary confusion related to the Argoaic and Artuli comments.<br /> 1. These are in reality distractions from the central issue that the original NEJM paper remains uncorrected in NEJM as to shipping times. Although a secondary issue, also uncorrected is the "days" nomenclature that is the reason for confusion in the Argoaic and Artuli comments on this forum. Also uncorrected in the original paper is the exposure risk definition which were informed were also incorrect. Together, these issues controvert the conclusions of the original study.<br /> 2. The incorrect nomenclature for "days" in the NEJM paper as well as in a follow up work (Clin Infect Dis, Nicol et al.) inflates the number of "elapsed time" days. This has not been corrected by the original authors. We on the other hand have corrected this by providing the correct information in our preprint.<br /> 3. Dr. Argoaic seems to have been given a wrong and earlier version (10/26) of the data which, although contains a variable that is supposed to correct the above problem, does not. In fact one cannot come to any conclusion that there is a discrepancy based on this incorrect 10/26 version, unless you have some preconceived notion.<br /> 4. Other post hoc analyses reported in follow up works (including social media) by the original authors looking at time from last exposure, or using a pooled placebo group, although flawed for a several reasons, when examined closely, nonetheless support our conclusions that early PEP prophylaxis with HCQ is associated with a reduction of C19.

Detail:<br /> Any confusion about "days" would disappear once the original authors correct the NEJM June 2020 paper as well as a follow up letter in Dec 2020 Clin Infect Dis (see upper red graph in Nicol et al. pubmed.ncbi.nlm.nih.gov/332... "pubmed.ncbi.nlm.nih.gov/33274360/)"). These errors inflate the "DAYS" by 1 day because the nomenclature for describing "days" was incorrect. As far as we know those corrections have not been made in the journals where these errors appear and in a way that can be retrieved in pubmed etc..

As far as we can tell, anyone who has cited the NEJM paper (NIH guidelines, NEJM editorial, many meta-anlayses etc., our protocol in preprint version) also misunderstood the "days" to mean the inflated figure. So the authors need to correct this. As far as we know we are the only ones to do this. After we were informed of this error by the PI (who was unaware of the problem himself) we described this problem very clearly in our preprint, distinguishing between elapsed time and the day on which a study event occurred. For the benefit of those who remain confused, we will endeavor to make it even clearer in a future version. You can read our correspondence log referenced in the preprint to verify that the incorrect "days" nomenclature was unknown to the PI, at least until 10/27 when he informed us about it.

You are confusing "DAY ON which an event occurred" with "DAYS FROM when an event occurred." For example the original NEJM Table 1 says "1 day, 2 days etc." for "Time from exposure to enrollment". This falsely inflates the number of elapsed time days by 1, and as the authors informed us (documented in our preprint), this really means DAY ON which enrollment occurred, with Day 1 = day of exposure, so you need to subtract 1 from the days to get elapsed time FROM exposure. The same error is repeated in Nicol et al. (note: we discuss other unrelated issues relating to time estimates in our preprint).

To confuse matters further, the problem is not even corrected in the dataset linked (datestamp 10/26/20) in the Argoaic comment. In column FS there is a variable "exposure_days_to_drugstart." This appears to indicate elapsed time (ie DAYS FROM) when it actually means the "DAY ON" nomenclature. We were only informed of the nomenclature error on 10/27/20 and later provided with a new version of the dataset on 10/30 where an additional variable "Exposure_to_DrugStart" (column GR) was provided that corrects this error by subtracting 1 from all the values.

Why the Argoaic comment does not link to the correct 10/30 version is unclear, but in this incorrect 10/26 version, the values for the new variable "Exposure_to_DrugStart" (column GR) are IDENTICAL to those in the "exposure_days_to_drugstart" (column FS) variable (they should be smaller by 1). Accordingly, unless Drs. Argoaic and Artuli had a preconceived notion (without checking the data) that some alteration had occurred, it is impossible to draw such a conclusion (albeit one that is incorrect for other reasons) from this incorrect 10/26 dataset. A number of colleagues have downloaded the 10/26 dataset from the link provided in the Agoraic comment, and have verified this problem.

So in addition to the original data set released in August 2020, as well as the three revisions (9/9, 10/6 and 10/30) we describe in our preprint there is this incorrect 10/26 version. I don't know how many people this affects but it would be appropriate for them to be notified that the version they have may be an incorrect one. An announcement on the dataset signup page covidpep.umn.edu/data would also be in order (nothing there today).

Regarding the possibly higher placebo rate of C19 on numbered day 4 (18.9%). This is matched by a commensurate change in its respective treatment arm, yielding RR=0.624 similar to that for numbered days 2 (0.578) and 3 (0.624), justifying pooling. We don't know if the 18.9% represents normal variation or has biological meaning.

Although they used enrollment time data (completely irrelevant to considering whether or not early prophylaxis is beneficial), the original authors (Nicol et al.) in a post hoc analysis, used a pooled placebo cohort to compare daily event rates (red bar graph). This would mitigate possible effects of an outlying value in the placebo cohort. We applied this same pooled placebo method to the data that correctly takes into account shipping times. This method is still limited because it may obscure a poorly understood relationship between time and development of Covid-19. Although at best this would be considered a sensitivity analysis, we did it to answer the Artuli question. This approach yields the same trends as our primary analysis. Using 1-3 days elapsed time of intervention lag (numbered days 2-4) for Early prophylaxis, there is a 33% reduction trend in Covid-19 associated with HCQ (RR 0.67 p=0.12). Taking only 1-2 days elapsed time intervention lag, we obtain a 43% reduction trend (RR 0.57 p=0.09). This analysis appears to reveal a strong regression line (p=0.033) of Covid-19 reduction and intervention lag.

We also looked at the post hoc analysis provided by the original authors (Nicol et al.) that used “Days from Last Exposure to Study Drug Start,” a variable not previously described in the publication, protocol or dataset, so we have no way of verifying it from the raw data. As in a similar PEP study (Barnabas et al. Ann Int Med) this variable has limited (or no) value, as we are trying to treat as quickly as possible from highest risk exposure, not an event (ie Last Exposure) that occurs at an undefined time later. (even the use of highest risk exposure has some limitation, which the authors pointed out to us and which we discuss in our preprint). Further the Nicol analysis used a modified ITT cohort, rather than the originally reported ITT cohort. with these limitations, pooling data for days 1-3 and comparing with the pooled placebo cohort (yields a trend reduction in C19 associated with HCQ (it is unclear which "days" nomenclature is used) after last exposure from 15.2% to 11.2% (RR 0.74, p=0.179).

Taken together with these "sensitivity" analyses inspired by the original authors' methodology, suggests that this is not an artifact of subgroup analysis. It could be said that any conclusions made by the sort of analyses conducted by Nicol are equally prone to the "subgroup artifact" problem. (also note that in our paper, the demographics for placebo and treatment arms in the early cohort match well).

Mention has been made elsewhere of two other PEP studies (Mitja, Barnabas) which concluded no effect of HCQ. It is important to note that the doses used in these studies were much lower than those used in the Boulware et al. NEJM study. Further, according to the PK modelling of the Boulware group (Al-Kofahi et al.) these doses would not have been expected to be efficacious (the Barnabas study used no substantial loading dose). So citing the Mitja and Barnabas studies to support claims of HCQ inefficacy in the Boulware et al paper is unjustified. On the contrary, taken together three studies suggest a dose-response effect. We discuss this in detail in our preprint.

Lastly it is important to note the since the original NEJM study was terminated early, the entire original analysis can be thought of as a subgroup analysis, with all of the attendant problems referenced by the original authors (and us). There is certainly a great deal of under powering and propensity to Type 2 errors, among the issues inherent in a pragmatic study design. The study was not powered as an equivalence study and so no definitive statement can be made that the HCQ is not efficacious. Along with the still uncorrected (in the original journal) issues of shipping times, "days" nomenclature and exposure risk definitions, there are are certainly many efficacy signals that oppugn the original study conclusions,and controvert the statement made in a UMN press release (covidpep.umn.edu/updates) "covidpep.umn.edu/updates)") that the study provided a "conclusive" answer as to the efficacy of HCQ.

_________________<br /> Please note that despite our offer to Dr. Argoaic to contact us directly to walk though the data to try to identify any issues, we have not been contacted.That offer is still extended to anyone who remains confused. We have also attempted to locate both Drs. Argoaic and Artuli to try to clear up their confusion, but these names do not exist in the mainstream literature (i.e pubmed, medrxiv), nor do they appear to have any kind of internet footprint.

With regard to Table 1 of our preprint, the reason why there are no patients for “Day 1” is that there were no patients who received drug the same day as their high-risk exposure. This is consistent with the PIs comment on 8/25/20 (p10 of email log) (at a time when he thought that there was a “Day zero”) “Exposure time was a calculated variable based date of screening survey vs. data of high risk exposure. Same day would be zero. (Based on test turnaround time, I don’t think anyone was zero days).”

We notice an obvious typo in the heading for the second column of our Table 1, which says “To”. But it should say “nPos”, to match the 5th column (and other tables). It is patently absurd that there should be a category of “1 to 0” days or “7 to 5” days etc. “From” makes no sense either and these typos have absolutely no effect on the analysis, interpretation or conclusions. This will be corrected in a later version.

On 2025-11-30 17:00:32, user Cyril Burke wrote:

RESPONSE TO REVIEWER #2<br /> June 27, 2022<br /> Reviewer #2: Thank-you for the opportunity to review this work which highlights the importance of monitoring serum creatinine over time and how this can be a useful tool in detecting possible CKD. This is an important topic as the use of sCr on its own is certainly under-utilized and changes are often missed because they don’t fall into a predefined category.<br /> Thank you for considering our manuscript and for your detailed comments.

MAJOR CONCERNS

A. “Choi- rates of ESRD in Black and White Veterans” doesn’t fit with the rest of the paper including the title; the introduction and conclusion also don’t adequately address this portion of the paper. It feels disjointed from the main point of discussion which is the use of sCr in screening “pre-CKD”. This section and discussion should be removed and possibly considered for another type of publication.<br /> We have attempted to clarify this inclusion. This manuscript could be divided into three or four short papers, increasing the likelihood that any one of them would be read. However, different groups tend to read papers about screening for kidney impairment, racial disparities, cofactors in modeling physiologic parameters, or policy proposals to encourage best practices. Despite the appeal of perhaps three or four publications, we decided to tell a complete story in a single paper, but we are open to suggestions.

Black Americans suffer three times the kidney failure of White Americans. Other minority groups also have excessive rates of kidney disease. However, analysis of Veterans Administration interventions can bring that ratio close to one, similar interventions might also reduce to parity the risk for Hispanic, Asian, Native Americans, and others. Within-individual referencing should allow better monitoring of all patients and help to reveal the circumstances and novel kidney toxins that lead to progressive kidney decline. The ability to identify a healthy elderly cohort with essentially normal kidneys would help to calibrate expectations for all. Better modeling of GFR should help everyone, too.

Over eight decades, anthropologists have had little scholarly success in diminishing the inappropriate use of ‘race’. Keeping these parts together may be no more successful, but we feel compelled to try.

B. Cases 1 - 3, (lines 93 – 122): where are these cases from? There is no mention of ethics to publish these patient results, which appears to be a clear ethics violation. If so, these cases should be removed and patient consent and ethical approval obtained to publish them.<br /> The authors describe the reasons for not obtaining an ethics waiver for this secondary data analysis. Despite this, the relative ease of obtaining an ethics waiver for secondary data analysis usually means that this is done regardless.<br /> We take patient privacy seriously and have completely de-identified the Case data, as required by Privacy Act regulations. We understand that no authorization or waiver was necessary. We discussed the issues with an IRB representative, reviewed the relevant regulations, and confirmed no need for formal review of a secondary analysis of already publicly available IRB-approved data or of completely de-identified clinical data collected in the course of a treating relationship.

IRBs have a critical role to play, but many (including ours) are overworked. We understand the impulse authors feel to gain IRB approval even when the regulations clearly do not required it. As we discuss in the revision, there is a more significant matter that IRBs could help to resolve if they have the resources to do so. For all of these reasons, and even though we, too, felt the urge to obtain IRB approval, we resisted adding “just a little more” to their work.

C. The message of the article and data representation is unclear: do the authors wish to show that sCr is superior to eGFR in this “pre-CKD” stage, should both be used together? Do the authors wish to convey that a “creatinine blind range” does not exist? Or is the aim to demonstrate that continuous variables should not be interpreted in a categorical manner?<br /> Our interest is detection and prevention of progression of early kidney injury at GFRs above 60 mL/min – a range in which eGFR is especially unreliable. We have advanced the best argument we can to detect changes in sCr while kidney injury is still limited and perhaps reversible. If experience reveals that some avoidable exposure(s) begins the decline, then clinicians might alert patients and thereby reduce kidney disease. How best to use longitudinal sCr remains to be determined from experience. However, our message is that early changes in sCr can provide early warning of a decline in glomerular filtration. We are confident that clinicians can learn to separate other factors that may alter sCr, as we do for many other tests.

MINOR CONCERNS<br /> ABSTRACT<br /> A. Vague. Doesn’t give a clear picture of the study<br /> We have tried to clarify the title and abstract and are open to further suggestions.

INTRODUCTION<br /> B. 51 – 57: needs to state that these stats are from e.g. the US. The authors should consider adding international statistics to complement those from the US.<br /> We have updated the statistics on death rates from kidney disease to include US and global data.

C. 68: reference KDIGO guidelines, state year<br /> We now reference the KDIGO 2012 guidelines.

D. 75 – 77: is this reference of the New York Times the most appropriate?<br /> We have expanded this section with peer-reviewed, scholarly references. However, we found Hodge’s summary of the issue succinct and hence potentially more persuasive for some than decades of scholarly references that have had limited or no effect in the clinic.

E. 82: within-individual variation not changes (this is repetition of the point made in lines 425 – 427, but should match the language)<br /> We have matched the language.

F. 82 – 84: reference? If this is a question it should be presented as such<br /> We have attempted to clarify this statement.

G. 84: “normal GFR above 60” = guidelines (including KDIGO) do not refer to 60 as normal GFR, 60 – 89 is mildly decreased. (see line 126)<br /> We agree and have corrected the language.

H. 93: avoid the use of emotive words such as apparently (also in line 428)<br /> We wanted to emphasize appearance without proof and have made these changes.

I. 94: “Not meeting KDIGO guidelines”: KDIGO 2.1.3 includes a drop in category (including those with GFR >90). This would appear to include some of the cases listed. Additionally, albuminuria should have been measured for case 2 and 3.<br /> We have clarified that cases may or may not fit KDIGO categories, though that question will frequently arise in evaluating sCr changes. Where available, we have added urine protein and/or albumin results to the Cases.

J. 97: “progressive loss of nephrons equivalent to one kidney”: this is based on a single creatinine measurement.<br /> Since the original submission, we discovered for this Case (now Patient 3) early serum creatinine results and notes indicating a six-month period off thiazide diuretic. This data clarified the baseline and showed a remarkable effect of thiazide diuretic on sCr. We have added follow-up sCr results and details of thiazide use to the ASC chart.

K. 93 – 122: Could any of these shifts be explained by changes in creatinine methodology or standardization of assays, especially over 15 – 20 years (major differences between assays existed before standardization and arguably still exist with certain methods).<br /> It would be useful to see a comparison between serial sCr and eGFR measurements on the same figure. There appears to be significant (possibly more pronounced) changes when eGFR is used. As line 87 mentions changes in eGFR may be as useful (and in some situations more useful) than changes in sCr alone.

It would be helpful to have a chronology from each local laboratory with the date of every change in creatinine assay or standardization. However, any single shift draws attention but does not necessarily indicate significant change in glomerular filtration. After one or several incremental increases, over at least three months, the sCr pattern may meet the reference change value (RCV) that signals significant change. In the future, from age 20 or so, a patient’s medical record should retain the full range of the longitudinal sCr for true baseline comparison.

As noted in the revised manuscript, Rule et al showed that there is measurable nephrosclerosis even in the youngest kidney donors, suggesting that some injuries (perhaps exposure to dietary toxins) may begin in childhood and that early preventive counseling may be worthwhile. Experience will show whether this can slow progression to CKD. As we note, quoting Delanaye, sCr accounts for virtually 100% of the variability in eGFR equations based on sCr (eGFRcr), and these equations add their own uncertainties, so no, we do not believe that eGFR is more useful than sCr when GFR is above 60 mL/min and possibly much lower as well.

We have added eGFR results to the ASC charts (in blue), though availability was somewhat limited.

L. 127 – 142: should there be separate charts for males and females, the differences in creatinine between males and females needs to be discussed somewhere in the paper.

We do not think there should be separate charts for men and women based on size. The role of sex in eGFR equations is mainly based on the presumption that the average woman has less muscle mass than the average man. Clinicians care for individuals, not averages, and this sweeping generalization that increases agreement of the average of a population introduces unacceptable inaccuracy to individual care. Within-individual comparison eliminates the need for assumptions on relative size or muscle mass. Major changes in an individual’s muscle mass will usually be evident to the clinician who can adjust for them.

However, reports suggest significant influence of sex hormones on renal function, including effects of estrogen and estrogen receptors, such as reducing kidney fibrosis, increasing lupus nephritis, and increasing CKD after bilateral oophorectomy. The mechanism of these effects and how they might be incorporated into eGFR estimating equations is unclear, but the effort may benefit from a more individualized approach with focus on a measurand rather than matching population-based averages of a quantity value (calculated from measurands).

M. Similarly, is this suitable for all ages?<br /> We think so. Another sweeping generalization based on age merely introduces another inaccuracy which complicates the task of clinicians caring for individuals. Older persons have varying health, athleticism, muscle mass, dietary preferences, etc. Rule et al reported that biopsies of about 10% of older kidney donors had no nephrosclerosis. Within-individual comparison eliminates the need for assumptions on relative muscle mass or inevitable senescent decline in nephron number. We substitute the assumption that any change in an individual’s muscle mass will be evident and can be accounted for. A seemingly ubiquitous risk factor, or factors, starts injuring kidneys at a young age, which we may yet identify.

N. 162 – 163: rephrase<br /> Done.

METHODS<br /> O. 185 – 193: aim belongs in the introduction, can be adjusted to complement paragraph 178 – 182.<br /> Reorganized and rewritten.

P. 196 – 205: reference sources

References provided.

Q. 224 – 247: not in keeping with the rest of the article or title and conclusion

We have revised and restructured this section.

RESULTS<br /> R. If eGFR is treated as a continuous variable does inverted sCr still have higher accuracy?<br /> We believe so. Serum creatinine is a measurand and reflects the total sum of physiologic processes, known and unknown. In contrast, eGFR equations yield a quantity value, calculated from a measurand and dependent on the assumptions and approximations incorporated by their authors. The eGFR equations are thus necessarily less accurate than the measurands they are derived from, in this case, sCr. In a hyperbolic relationship, as the independent variable drops below one and approaches zero, the effect is to amplify the inaccuracy of the independent variable in the dependent variable. By avoiding the mathematical inverting, the data suggest that direct use of sCr is far more practical for pre-CKD.

S. As mentioned, the section on ESRD in black and white veterans doesn’t fit in with the rest of the article.<br /> We have revised, reorganized, and rewritten. We also outlined our rationale above.

DISCUSSION<br /> T. As mentioned, section 4.1 doesn’t fit in with the rest of the article. As the authors note the correlation between illiteracy and CKD is likely not causal.<br /> See above.

U. 387: erroneous creatinine blind range. The data presented does not show this is erroneous there is still a relative blind range. A distinction must be made between a population level “blind range” and an individual patient’s serial results. The data and figure 4 in particular demonstrate the lack of predictive ability of sCr above 40ml/min compared to below 40ml/min at a population level. For an individual patient this “blind range” is more relative, and a change in sCr even within the normal range may be predictive. (Note: the terminology “blind range” is problematic).<br /> We agree. On reading closer, Shemesh et al call attention to “subtle changes” in serum creatinine even though they had access only to the uncompensated Jaffe assay, so their recommendation to monitor sCr is even more forceful, today, due to more accurate and standardized creatinine assays. We have attempted to clarify this in the manuscript.

V. 399 – 400: “rose slowly at first and then more rapidly as mGFR decreased below 60” this refers to a relative blind range. Whether these slow initial changes can be distinguished from analytical and intra-individual variation is the question that needs to be answered before we can say a “blind-range” doesn’t exist for an individual patient.

We appreciate this observation. We believe longitudinal sCr is worth adopting to gain insights into individual sCr patterns, which may reveal early changes in GFR, among other influences on sCr. This is a low-cost, potentially high-impact population health measure, and there seems little risk in trying it because many clinicians already use components of the process.

W. 425 - 432: sCr is indeed very useful when baseline measurements are available. eGFR remains useful when baseline sCr is not available or when large intervals between measurements are found.<br /> As Delanaye et al noted, virtually 100% of the variability in longitudinal eGFR is due to sCr, so we understand that the errors in eGFR can be (and usually are) greater than but cannot be less than those in sCr.

X. 425: low analytical variation- if enzymatic methods are used<br /> Lee et al suggest that even the compensated Jaffe method provides some accuracy and reproducibility, which may allow longitudinal tracking of sCr even where more modern assays are as yet unavailable.

Y. 428: avoid the use of “apparently”<br /> Done.

Z. 430: reference 56 compares sCr and sCysC with creatinine clearance NOT with mGFR, this does not prove that mGFR has greater physiologic variability. Creatinine clearance is known to be highly variable (partially due to two sources of variability in the measurements of creatinine: serum and urine).<br /> The creatinine clearance is another form of mGFR, and our understanding of it begins with the units: if the clearance or removal of creatinine were being measured, the units should be umoles/minute, but they are mL/min. “Clearance” is an old concept coined by physiologists to describe many substances, such as urea, glucose, amino acids, and other metabolites. Since creatinine is mostly not reabsorbed and is only slightly secreted in the tubules, the “creatinine clearance” became a measure of GFR. The ratio of urine Creatinine to serum Creatinine is simply a factor for how much the original glomerular filtrate then gets concentrated (typically about 100-fold) by the kidney. Since the assumption is that the timed urine was once the rate of glomerular filtrate production, the creatinine clearance is a measure of the GFR.

Creatinine clearance has some inaccuracies based on tubular secretion, but also has some advantages: blood concentrations are essentially constant during urine collection, no need for exogenous administration, and reliable measurements in serum and urine. The methods that we often call mGFR also have problems, including unverifiable assumptions about distributions, dilutional effects, and others we cite in the text. None of these are direct measures of GFR. Due to changes in remaining nephrons, even true GFR itself is not strictly proportional to the lost number of functional nephrons, which seems the ultimate measure of CKD that Rule et al estimated from biopsy material.

AA. The limitations of sCr for screening should also be discussed: differences in performance and acceptability between enzymatic and Jaffe methods (still widely used in certain parts of the world), the effect of standardizing creatinine assays (an important initiative but one that could also produce shifts in results around the time of standardization- see cases), low InIx means that once-off values are exceedingly difficult to interpret, is a single raised creatinine value predictive (or should there be evidence of chronicity): similarly are there effects from protein rich meals, etc (The influence of a cooked-meat meal on estimated glomerular filtration rate. Annals of Clinical Biochemistry. 2007;44(1):35-42. doi:10.1258/000456307779595995)<br /> We have added discussion of additional references on reproducibility of sCr assays and discuss dietary meat and, in Part Three, possible dietary kidney toxins.

CONCLUSION<br /> BB. The discussion recommends using SCr above eGFR while the conclusion recommends the NKF-ASN eGFR for use in pre-CKD and ASC charts. While the use of both together in a complementary fashion is understandable- this needs to be congruent with the discussion, aims and results.<br /> We have rewritten this section. We would welcome any further recommendations.

Cyril O. Burke III, MD, FACP

On 2025-11-30 16:56:07, user Cyril Burke wrote:

RESPONSE TO REVIEWER #1

June 27, 2022<br /> Re: Longitudinal changes in creatinine signal early decline in glomerular filtration rate without consideration of age, sex, ‘race’, and nationality

We greatly appreciate that the reviewers were thorough, fair, and helpful in their comments.

Comments to the Author

Reviewer #1: Burke et al submit a somewhat unusual paper, devoted to a topic of potential major clinical relevance, and as yet understudied.

General comments

1. The thesis of the authors, that using the baseline serum creatinine of a given patient would potentially improve the earlier diagnosis of kidney disease, even in the normal range, is in line with the experience of this reviewer, who always retrieves, whatever the difficulty of reaching that goal, past results of blood tests, and uses them as a way to date the onset of kidney disease, sometimes with important prognostic implications.

Your experience adds support to the literature suggesting that historical sCr levels provide a context for sCr changes. These benefits might encourage investments in digital data exchanges so that electronic health records (EHRs) can ease collection and presentation of sCr results from multiple commercial and hospital laboratories.

2. Yet, the authors do not provide data strongly supporting their thesis. For instance, when looking at case 2 [now Patient 3], should the last point (the most recent one) be omitted, there would be very little evidence supporting progressive early kidney disease.

We advocate prospective monitoring of longitudinal sCr as a proxy for glomerular filtration rate (GFR). The Cases were meant to show that charting the data and simple follow-up over several visits and months can allow general clinicians to differentiate CKD from other explanations for increased sCr. The four case histories represent patients in a non-nephrology medical practice with borderline eGFR that raised the possibility of CKD. In each of these cases, retrospective collection of sCr values suggested varied explanations for the elevated sCr, and we expect many cases will represent sCr influences other than CKD, not necessarily warranting nephrology referral. Armed with this tool, and used prospectively, Physicians, nurse practitioner, and physician assistants (PCPs) might identify and manage the 90% of patients with currently unrecognized CKD.

3. The claim that the statistics fit the data better when all points are used (page 9,11) should not come as a surprise. Using thresholds instead of the full range of values has long been known to be more powerful for statistical analysis. But fitting the data does not equal to a high positive predictive value!

We agree that this is counterintuitive, so we thought this was an important point to discuss. Research methods that get translated into clinical settings rely on assumptions that are not always familiar to healthcare workers. Whatever the merits of thresholding conventions, understanding their mathematical underpinnings can inform a more nuanced interpretation of lab results. The revision includes our initial, intuitive assessment of the data and the interpretation of the residuals – from a mathematics perspective. Lack of awareness about residuals can easily lead to improper interpretation of thresholded lab data. The use of statistics is not intended to document superiority of fit but rather to demonstrate how simplifications with practical clinical value may gloss over clinically relevant information in some cases. The inclusion of additional charts seeks to take it away from abstracted statistics and toward more intuitive clinical concerns. We favor early diagnosis of kidney injury through investigation of nonspecific changes in longitudinal sCr. This method seems usable and may be manageable by PCPs using a time frame of several visits over several months to separate false positives, which may be influenced by chance attributable to the mathematical properties of lab data.

4. A key question is whether in a real-world context, the earlier diagnosis of kidney disease would be possible, without too much background noise from intercurrent illness (functional), drugs (NSAIDS, etc.). In other words, would the specificity (or PPV) of the suspicion of early kidney disease be reasonable enough to catch the attention of clinicians

We think so. We believe longitudinal serum creatinine (sCr) will encourage dialogue between patients and clinicians, raising awareness of the importance of avoiding kidney injuries that often happen out of sight and out of mind until, for far too many, culminating in urgent dialysis. In the same way that patients now ask for their blood pressure, we anticipate patients tracking their own sCr and kidney risks. Decades after introduction of the mercury sphygmomanometer, PCPs learned how to manage blood pressure to improve health. We believe longitudinal sCr can soon be a widely used tool because the concepts are old, there is a broad literature supporting this approach, and the value can be enhanced by more frequent testing of sCr. This is what PCPs do – sort the random cough, costochondritis, or stress response from nascent pneumonia, angina, and hypertension. PCPs already worry about the kidneys. They may welcome a tool to accompany the chest radiograph, electrocardiogram, and sphygmomanometer.

Of interest, the decision analysis by den Hartog et al found markedly more false-positive diagnoses of CKD with eGFR than with serum creatinine alone.

5. Even though there has been improvement in the standardization of measurement of serum creatinine (IDMS), the comparability of results measured by different labs remains suboptimal, at least in the experience of this reviewer, and medical shopping is not uncommon, making the availability of all previous results in the same graph a logistical challenge.

We share this concern, which laboratorians have wrestled with for many years and will not be solved soon. However, we propose utilizing the maximum serum creatinine (sCr-max) to smooth the variability of these inputs (as well as the variability from patient diet and hydration). One laboratory will be the highest, and when patients use multiple laboratories, one laboratory may more often define the sCr-max. As patients learn the rationale for using the same lab, we believe most (not all) will voluntarily use one or perhaps two labs (as they mostly do when we repeating longitudinal MRI imaging studies, for example). The sCr-max reduces the effect of variability between laboratories, allowing clinical insights even without future improvements in sCr assays.

Australia, Canada, and the United Kingdom have stricter sCr analytical performance goals than the United States, which could improve its sCr comparability by matching their standards.

Specific comments

1. The authors should mention that the USPTFS decided a month ago to revisit the question of screening for kidney disease in high-risk groups (page …)

One reference stated that this initiative has not been announced publicly but is “under active consideration” by USPTFS because “…for a screening to help people live longer, healthier lives, clinicians must be able to treat the condition once it is found. The existence of effective treatments is one of many important factors that the Task Force considers.” This perspective is surprising because it ignores the potential of effective prevention by avoiding NSAIDs, hypotension, dehydration, and nephrotoxic medical treatments (e.g., aminoglycosides). We, too, look forward to updated findings from USPTFS.

2. Even though ESRD has a legal meaning in the USA, not very relevant to the topic of this paper about early kidney disease, the authors should stick to the nomenclature proposed by a recent KDIGO consensus conference (see Levey et al. Nature Reviews in Nephrology). In particular, use kidney failure instead of ESRD/ESKD. When the topic is glomerular filtration, use that wording instead of kidney function (page…)

We have adopted this terminology and would welcome any further recommendations.

3. The authors allude to the concepts of prediabetes and prehypertension. But this reviewer points to the fact that the levels used to define those entities are currently “generic”, rather than based on previous values in an individual subject. Please discuss.

We understand that the normal population ranges for serum glucose and blood pressure are narrower, with less interindividual variation, so population reference ranges work well for monitoring diabetes mellitus and hypertension. Unfortunately, this is not true for serum creatinine, though within-individual reference of longitudinal sCr appears to facilitate diagnosis of pre-CKD.

4. The authors repeatedly mention in the discussion section evidence that even small increases in serum creatinine have prognostic significance. This has indeed been known for decades but is a different topic: AKI. Admittedly, there is growing evidence that AKI and CKD are linked. But that the stability of a biological parameter is prognostically best is all except surprising: the same is true for body weight, mood, blood pressure etc.

We agree that AKI and CKD appear to be merging and this may become clearer from more frequent sampling and charting of longitudinal sCr. What has been missing is graphical representation of the data to allow quick assessment for CKD in long-term trends, and this may soon be obtainable from EHRs and IT departments, which should end the practice of deleting historical data of value to longitudinal analysis.

[See next comment for Response to Reviewer #2.]

On 2025-11-30 23:44:45, user Cyril Burke wrote:

[Note: This is the second of several rounds of review of an earlier version of our combined manuscript, aiming to reduce ‘racial’ disparity in kidney disease. The comments were kindly offered by nephrologists, through a medical journal, and we remain grateful to them for the time and care they gave to improve our manuscript.

We removed identifying features and included our responses, at the end of this comment. The changing title and line numbers refer to earlier versions.]

August 3, 2022<br /> Dear Dr. Burke III,

REDACTED.

Reviewer #1: Cyril O Burke III et al submit a revised version of their intriguing , unusual paper.

Overall, the paper remains extremely lengthy (the total , including clean and track versions and reply to reviewers is close to 200 pages !!) , whereas it contains relatively little original data.

The authors speculate and comment a lot (and most of these speculations/comments will hardly be understandable by the expected audience, primary care physicians), and this will in addition distract the reader from the main key message (which is right in the opinion of this reviewer (see first round of review) and warrants more attention and studies.

The race part is irrelevant for the key point (race does not change over time, and thus is not relevant when looking at longitudinal serum creatinine or eGFR) and should be deleted in the opinion of this reviewer. In this respect, I completely agree with the comment of reviewer 2 in the first round.

I can not resist quoting here the reply of the authors to reviewer 2. “This manuscript could be divided into three or four short papers, increasing the likelihood that any one of them would be read. However, different groups tend to read papers about screening for kidney impairment, racial disparities, cofactors in modeling physiologic parameters, or policy proposals to encourage best practices. Despite the appeal of perhaps three or four publications, we decided to tell a complete story in a single paper, but we are open to suggestions.”

My reply to their reply: nobody would read the current paper , even partially. Shorten, shorten, shorten please and focus on the key message.

Reviewer #2: Thank-you, once again, for the opportunity to review this lengthy “thesis-style” manuscript which discusses some important often over-looked topics. The under-use of serial creatinine measurements and over-reliance on often erroneous eGFR measurements is an important point which is easily missed by healthcare workers with potentially serious consequences. Likewise, the misuse of racial constructs in medicine (and elsewhere) is an important point.

I am satisfied with this re-submission and the changes which have been made to the original manuscript.

Minor points:<br /> 431: “creatinine inhibits several membrane transporters”. = Cimetidine

502: “Because mGFRs have population variation as wide as sCr, with much greater physiologic variability compared to the relatively stable sCr and serum cystatin C”<br /> As mentioned previously the cited article compares the variability of sCr and cystatin C with CrCl, I agree with the authors that CrCl is a form of mGFR, however, probably one of the poorer forms and not what a reader will think of when mGFR is mentioned. In our current age of medicine when we talk about mGFR CrCl is seldom included, studies reviewing methods of mGFR will seldom include CrCl, however CrCl may be compared to one of the mGFR methods. Likewise, if a patient is sent for a mGFR, a CrCl will not be performed. In our current age of medicine mGFR refers to methods such as the clearance of iohexol, iothalamate, Cr-EDTA, inulin, DTPA, etc; the authors themselves mention this (line 539 – 540). I fully agree with the authors that mGFR is FAR from perfect and has many inaccuracies and imprecisions (which are often overlooked)- these are well published, some of which are cited in this manuscript. If the authors wish to use the current study as a source they should state the findings in a way that cannot be misinterpreted. For example: “CrCl has much greater physiologic variability than sCr and cystatin C …” – in this case the reader can determine for themselves whether they would use CrCl as a surrogate for mGFR. Alternatively, adjust the statement and use another source which has shown the variability that exists with what we currently refer to as mGFR method.

670 – 719: As the authors specifically discuss age it would be prudent to briefly mention the short-comings, or considerations for interpretation, of serial creatinine measurements at a very young age which generally rise until late adolescence when steady muscle mass is achieved. Also note changes in creatinine and GFR from birth till 2 – 3 years.

783 – 784: Consider re-wording the grammar makes this sentence difficult to read

959 – 968: Note, editing has not been accepted (tracked changes still shown)

1116 - 1121: “Using the opioid crisis as an example…. in, for example, the opioid crisis” – same sentence

RESPONSE TO REVIEWERS:<br /> September 17, 2022<br /> Longitudinal creatinine, not ‘race’, signals pre-chronic kidney disease and decline in glomerular filtration rate

We again greatly appreciate the reviewers for offering detailed comments and guidance, which we have endeavored to incorporate as best we could.

Comments to the Author<br /> Reviewer #1: Cyril O Burke III et al submit a revised version of their intriguing, unusual paper.<br /> 1. Overall, the paper remains extremely lengthy (the total, including clean and track versions and reply to reviewers is close to 200 pages !!), whereas it contains relatively little original data.<br /> The authors speculate and comment a lot (and most of these speculations/comments will hardly be understandable by the expected audience, primary care physicians), and this will in addition distract the reader from the main key message (which is right in the opinion of this reviewer (see first round of review) and warrants more attention and studies.<br /> The race part is irrelevant for the key point (race does not change over time, and thus is not relevant when looking at longitudinal serum creatinine or eGFR) and should be deleted in the opinion of this reviewer. In this respect, I completely agree with the comment of reviewer 2 in the first round.<br /> I can not resist quoting here the reply of the authors to reviewer 2.<br /> "This manuscript could be divided into three or four short papers, increasing the likelihood that any one of them would be read. However, different groups tend to read papers about screening for kidney impairment, racial disparities, cofactors in modeling physiologic parameters, or policy proposals to encourage best practices. Despite the appeal of perhaps three or four publications, we decided to tell a complete story in a single paper, but we are open to suggestions."<br /> My reply to their reply: nobody would read the current paper, even partially. Shorten, shorten, shorten please, and focus on the key message.<br /> We fundamentally agree and have worked to shorten the text; to clarify our understanding that ‘race’ may change with time, location, and self-identification; and to add a Table of Contents to make the Parts more accessible to interested readers. We comment a lot because, in highly racialized societies, like the US [1,2], it can be difficult to see beyond ‘race’ without explicit speculation about other possible explanations for difference, which we understand, may or may not pan out under investigation. One hope is that all clinicians will pursue explanations other than ‘race’, but this seems unlikely. Busy medical researchers have little time to develop expertise outside their area of interest, which may explain why ‘Commentary’ and ‘Perspective’ articles have failed to inspire an ethical ban on the misuse of ‘race’ in medical research, journals, clinics, and elsewhere [3]. We do not know whether a suite of articles can meaningfully contribute to ending misuse of ‘race’, where so many scholarly articles have failed, but after perceiving little change over four decades, trying something completely different seemed (almost) rational.

1. Nunez-Smith M, Curry LA, Bigby J, Berg D, Krumholz HM, Bradley EH. Impact of race on the professional lives of physicians of African descent. Ann Intern Med. 2007 Jan 2;146(1):45-51. doi: 10.7326/0003-4819-146-1-200701020-00008. PMID: 17200221.

2. Betancourt JR, Reid AE. Black physicians' experience with race: should we be surprised? Ann Intern Med. 2007 Jan 2;146(1):68-9. doi: 10.7326/0003-4819-146-1-200701020-00013. PMID: 17200226.

3. McFarling UL. Troubling podcast puts JAMA, the ‘voice of medicine,’ under fire for its mishandling of race. Stat News. 2021 April 6 [Cited 2022 August 31]. Available from: https://www.statnews.com/2021/04/06/podcast-puts-jama-under-fire-for-mishandling-of-race/ <br /> Reviewer #2: Thank-you, once again, for the opportunity to review this lengthy “thesis-style” manuscript which discusses some important often over-looked topics. The under-use of serial creatinine measurements and over-reliance on often erroneous eGFR measurements is an important point which is easily missed by healthcare workers with potentially serious consequences. Likewise, the misuse of racial constructs in medicine (and elsewhere) is an important point.<br /> Thank you for again giving time for helpful criticism and comments on our manuscript.

A. I am satisfied with this re-submission and the changes which have been made to the original manuscript.<br /> Minor points:<br /> B. 431: “creatinine inhibits several membrane transporters”. = Cimetidine<br /> Corrected.

C. 502: “Because mGFRs have population variation as wide as sCr, with much greater physiologic variability compared to the relatively stable sCr and serum cystatin C”<br /> As mentioned previously the cited article compares the variability of sCr and cystatin C with CrCl, I agree with the authors that CrCl is a form of mGFR, however, probably one of the poorer forms and not what a reader will think of when mGFR is mentioned. In our current age of medicine when we talk about mGFR CrCl is seldom included, studies reviewing methods of mGFR will seldom include CrCl, however CrCl may be compared to one of the mGFR methods. Likewise, if a patient is sent for a mGFR, a CrCl will not be performed. In our current age of medicine mGFR refers to methods such as the clearance of iohexol, iothalamate, Cr-EDTA, inulin, DTPA, etc; the authors themselves mention this (line 539 – 540). I fully agree with the authors that mGFR is FAR from perfect and has many inaccuracies and imprecisions (which are often overlooked)- these are well published, some of which are cited in this manuscript. If the authors wish to use the current study as a source they should state the findings in a way that cannot be misinterpreted. For example: “CrCl has much greater physiologic variability than sCr and cystatin C …” – in this case the reader can determine for themselves whether they would use CrCl as a surrogate for mGFR. Alternatively, adjust the statement and use another source which has shown the variability that exists with what we currently refer to as mGFR method.<br /> We appreciate this comment and have both added another reference and added to the text an argument for reconsidering creatinine clearance. Many hospitals and some countries lack the resources for advanced mGFR filtration markers, which are only used for research or for screening related to kidney transplants. However, most laboratories have the tools for ‘quick-creatinine clearance’ (quick-CrCl), which may be an acceptable alternative to the classic mGFRs. If confirmed, a simple and affordable quick-CrCl might allow hospitals and laboratories worldwide an alternative measurement requiring fewer assumptions for another aspect of glomerular filtration.

D. 670 – 719: As the authors specifically discuss age it would be prudent to briefly mention the short-comings, or considerations for interpretation, of serial creatinine measurements at a very young age which generally rise until late adolescence when steady muscle mass is achieved. Also note changes in creatinine and GFR from birth till 2 – 3 years.<br /> We have added a brief discussion of the diagnosis of CKD in infants, children, and adolescents.

E. 783 – 784: Consider re-wording, the grammar makes this sentence difficult to read<br /> Done.

F. 959 – 968: Note, editing has not been accepted (tracked changes still shown).<br /> Done.

G. 1116 - 1121: “Using the opioid crisis as an example…. in, for example, the opioid crisis” – same sentence.<br /> Rewritten.

We thank you.

On 2021-12-25 08:38:40, user Eslam Maher wrote:

The authors investigate whether Machine Learning (ML) algorithms fare better compared to traditional Cox models in big data. They selected Glioblastoma and gliosarcoma from SEER as the basis of their data set. There are two main points that are worth considering here, (1) statistical, and (2) clinical.

(1) a- Glioblastomas are relatively rare diseases, therefore, readers need to bare in mind that the hypothesis studied here may not be relevant to their work that is usually mono-institutional or multi-institutional. Unlike the huge SEER database, we never actually have such numbers at hand to analyze in survival models.

There is no doubt that Cox would outperform ML models in smaller samples. ML is gaining popularity in the medical community that is hugely inflated and unnecessary.

b- Unlike ML approaches, the performance of Cox models is heavily dependent on its assumptions. This includes the proportionality of hazards between levels of a given variable, which the authors do not seem to have investigated this assumption before running the model.

Another assumption is how the model was selected in the first place. The authors say they have run Cox univariably to decide upon the variables that would be used in the final mode. It is unclear whether a "significant" variable is considered as such at 5% alpha. Regardless of the alpha level, automated stepwise methods are notorious, this is because they are very popular among physicians and not professional statisticians and epidemiologists. Stepwise methods do not allow modelers to think about the model at hand. Plus, some causal variables may not be statistically significant, while some nuisance variables may be coincidentally significant due to high N. Automated regression using p-values is a bad idea because it also ignores multiplicity problems.

(2) a- 22.6% of the cases included had no surgery, how then were they diagnosed as glioblastomas if no tissue samples were available? It is unclear if surgeries comprised craniotomies and biopsies or the former alone.

b- All glioblastomas and gliosarcomas are grade IV tumors, however, for some reason, grade is a variable included in the models with levels of grade I, II, III, and IV!

c- Reference categories in the authors' models were selected alphabetically rather than clinically. For Site, there are 14 levels using ICD-O classifications. Such classifications are not meant for clinical correlations. For example, all Lobar sites (frontal, pariental, occipital etc) are part of the Cerebrum. There are only 2 cases available for cauda equina glioblastomas, which is nonsensical to include as a separate level in the model (which puts more constraints in the model's degrees of freedom while also resulting in unstable ratios).

d- Finally, the median survival for glioblastoma patients as noted by the authors was eight months. Looking for model accuracy at 120 months is just insane.

This would have a been a neat paper had the authors run a proper Cox model rather than run a straw man, and designed their study with a neuro-oncologist. Even then, please note that this preprint is concerned with the performace of these models IN BIG DATA only, so do not extrapolate to the data you are routinely working with.

On 2020-03-20 20:57:29, user Sylvie Vullioud wrote:

Could authors provide information to dissipate high risks of bias:

1. Manuscript was first published on mediterranee-infection.com website, not on medRxiv. On the manuscript on the website on mediterranee-infection.com, I can read 'In Press 17 March 2020 – DOI : 10.1016/j.ijantimicag.2020.105949'. It means that manuscript was already accepted by International Journal of Antimicrobial Agents at the time when the manuscript was deposit on the 20.03.2020 on medRxiv.

-> Pre-print on medRxiv is not a real pre-print to collect feed-back for manuscript improvement, as originally designed for. Moreover, medRxiv states: 'All preprints posted to medRxiv are accompanied by a prominent statement that the content has not been certified by peer review'.

-> There is an obvious potential conflict of interest, because last author Raoult is editor of the article collection COVID-19 Therapeutic and Prevention in International Journal of Antimicrobial Agents.

-> International Journal of Antimicrobial Agents is runned by Elsevier, suggesting 'If accepted for publication, we encourage authors to link from the preprint to their formal publication via its Digital Object Identifier (DOI)'.

1. Discussion on the controversy of main cited Chinese paper, ref 8 ?

2. According to paper, allocation of patients group was random but treated group is 51.2 years average and control group 37.3 years?

3. Article describes 3 conditions of patients: asymptomatic, low and high symptoms. Why?

4. Care to patients, biological and physiological sampling and analyses, and statistical analyses were not blinded. Why?

5. I think that no placebo was used. Why?

6. 6 patients on total of 42 were excluded from study: three patients were transferred to intensive care unit, 1 stopped because of nausea, 1 died. One left hospital. <br /> It is written :'study results presented here are therefore those of 36 patients (20 hydroxychloroquine-treated patients and 16 control patients). Why were dead, intensive care, and nausea patients not included in statistical treatment? <br /> -> This may be a selection bias? <br /> -> What about unwanted very worrying effects of the treatment?

7. 'The protocol, appendices and any other relevant documentation were submitted to the French National Agency for Drug Safety (ANSM) (2020-000890-25) and to the French Ethic Committee (CPP Ile de France) (20.02.28.99113) for reviewing and approved on 5th and 6th March, 2020, respectively'. Pre-print was posted on 20.03.2020. Time points on day 14 on patients.<br /> -> So recruitment and study started before approval of ANSM and French Ethic Committee? How is it possible?

8. How is it plausible that numerous authors (18!) participated equally to the work? Is it possible to add their respective contributions?

Thank you in advance for considering my questions. <br /> Regards, <br /> Sylvie Vullioud

On 2021-09-04 19:09:42, user Ben Veal wrote:

As a qualified statistician who's been doing this stuff for over 20 years, and has worked on several medical studies I think I ought to add my voice to the crowd.<br /> There may be a few things that aren't fully accounted for such as the false positive rate for PCR tests, or unbalanced populations due to deaths of highly vulnerable members of the pre-infected group, but they should not alter the conclusions much. As mentioned by others the false positive rate for PCR tests would have the effect of biasing the risk ratio downwards, not upwards, so we should expect the effect to be even stronger than reported.

As for the potential drop-out issue due to deaths of highly vulnerable people among the pre-infected group; this would only be a problem if there are some unaccounted for cofactors causing that high vulnerability. If this is the case then we can approximately correct for the imbalance by estimating the number of deaths in the pre-infected group based on the known infected mortality rate. <br /> I have done that calculation (see link below), and get a lower bound estimate for the 95% confidence interval of [4.3,11.23] which is still significant.<br /> However, it could make a big difference to the risk of hospitalization (again assuming there are some important cofactors unaccounted for).<br /> https://www.facebook.com/ec...

Another criticism I have read in these comments is that they should have used a conditional model (https://en.wikipedia.org/wi... "https://en.wikipedia.org/wiki/Conditional_logistic_regression)") to account for the matching. Actually a conditional model is used when there is unequal distribution of the treatment groups (pre-infected & vaccinated) within each strata (age, gender, socio-economic status & geographic region), and you are unable to use covariates to control for this. But the matching that they did ensures that this isn't the case. Furthermore they control for all but one of the strata (geographic region) with covariates.

So, overall I trust the overall conclusion; natural immunity from pre-infection is better than vaccination, but not as good as natural immunity + vaccination.

This does not mean governments should put a halt to their vaccination programs since that's obviously going to result in more deaths among the vulnerable, but perhaps it might be wise to reduce the vaccination rate among the less vulnerable people (i.e. young healthy people) so that they can build up natural immunity and be better prepared to fend off new variants from spreading through the population. In fact it ought to now be possible to estimate the optimal proportions of vaccinated & unvaccinated that would result in the lowest risk of contagion spread, given that we can expect to see this virus reappearing every year.

On 2021-09-14 13:39:06, user Henri van Werkhoven wrote:

Dear colleagues,

With interest did we read this manuscript which fueled a lively discussion during our journal club of the department of infectious diseases epidemiology at the University Medical Center Utrecht. The authors address a relevant research question. If there is a substantial difference in the risk of SARS-CoV-2 infections between previously infected and vaccinated individuals – as suggested - this may have consequences for social distancing, testing recommendations, and for projections of the impact of vaccination on future COVID-19 trends. However, we have several concerns regarding generalizability, selection bias, information bias, and confounding that we would like to address. We focus our discussion on model 1: the comparison of the fully vaccinated non-infected group (group 1) to the infected non-vaccinated group (group 2).

In regard to generalizability:<br /> - Due to the matching process, only 4% of the available data is used (i.e. for model 1 only 32430/736559) and as a consequence the study population is fairly younger (with expectedly less comorbidity) than the source population (i.e. vaccinated individuals, infected individuals). Therefore, the study population may not be representative of this source population which severely limits the external validity of results for all vaccinated/infected people.<br /> - Naturally, subjects who died due to previous SARS-CoV-2 infection were not included in the study. Yet, without information on morbidity and mortality and contribution to the spread of SARS-CoV-2 from the primary infection, the results of the study are not informative for the question whether people without previous SARS-CoV-2 infection should be vaccinated or await natural infection. <br /> - All three study groups – vaccinated or infected at baseline (28th of February) – were established upon future information (no infection, no additional vaccination after June 1, 2021), which severely limits the use of the results for today’s decision making.

In regard to selection bias:<br /> - People with a SARS-CoV-2 infection between February 28, 2021 and June 1, 2021, or those who received a first (infected group) or third vaccine (vaccinated group) between February 28, 2021 and August 14, 2021 were excluded from this study. Thus the study population of group 2 consists of previously infected people that do not take the opportunity to receive a booster vaccine, which may well be the less vulnerable people with a lower baseline risk of getting infected/hospitalized. This would bias the estimate in favor of the infected group.<br /> - Similarly, though at a smaller scale, people who died from COVID were not included in the analysis. This decreases the vulnerability of the infected group for secondary infections and/or hospitalization. This too would bias the estimate in favor of the infected group.

In regard to information bias:<br /> - A difference in willingness to test between the vaccinated and previously infected group can result in biased estimates. Vaccinated people may be more on guard in regard to COVID-19 symptoms (especially if they adhere less to regulations because they are vaccinated) and will be tested more frequently. This can bias the estimate, again in favor of the infected group. However, this form of bias should not have affected the outcome hospitalization due to COVID-19, for which differences had the same direction. Yet, the number of those endpoints was low, limiting statistical power.

In regard to confounding:<br /> - The authors acknowledge absence of information about health behavior, such as social distancing and masking. If the vaccinated group would adhere less to these preventive measures due to a sense of safety, this would also bias the estimates in favor of the infected group.<br /> - A potential important aspect is the young average age (36 years) of the study population. As they were all fully vaccinated before February 28th, we thought that a large proportion may have been health care workers, who have a higher chance of exposure to SARS-CoV-2, and thus infection after vaccination. This would also bias the estimate in favor of the infected group.

We have scrutinized the paper in search of the fatal flaw; the one major methodological limitation that could explain the extreme effect in favor of the infected group, as reported. We conclude that it is not there, as we don’t think that any of the above biases can explain all of the effect. However, we did found several weaknesses that each have the potential to yield a modest bias, all in the same direction. Five modest biases may yield a large effect estimate. We, therefore, consider the question whether natural immunity provides better protection than full vaccination with Pfizer/BioNTech’s COVID vaccine remains unanswered.

The authors (Annemarijn de Boer, Valentijn Schweitzer, Marc Bonten and Henri van Werkhoven, all at University Medical Center Utrecht) acknowledge all other journal club participants for their time dedicated to discussing the paper.

On 2021-12-13 22:59:33, user Just Because I can wrote:

Greetings RI team from Utah! I must begin with nicesties; "Go BRUNO"! My son graduated this past May 2021 from Brown. I am a speech and language pathologist with over 30 years of hospital, private and public school setting experiences. Over the past nine years, I have professionally focused on children ages 3-5 within the public preschool and private therapeutic settings. I service students and their parents with the most intensive and restrictive learning environments within our District due to cognitive, behavioral and communicative delays. I can't help but weigh in now, as I previously shared this article with my peers in August as I braced for the impact of the 2021 school year.

Given your single assessment tool (I professionally do not profess strong decisions based on a single evaluative instrument, even as widely accepted at the Mullen), I've found your results to be intriguing and frankly, just as we anticipated.

To compare to RI, our school district, closed schools for Remote Learning for only 3 mos. in the Spring of 2019 and returned to in person instruction with hybrid options in 2020. Of a caseload of 65 students, I had 3 that were online/virtual. In 2021, our District returned to essentially all in student learning.

My informal observations this school year in Utah has been as follows:

1. Increase in new referrals and eligible "older" 4+ year old children scoring remarkably delayed communication (Standard scores <50 given a typical range of 85-115) and no previous history of EI or preschool interventions. Our TIER 3, most restrictive preschool program has a marked influx of new referrals (e.g., total students in May was 24 and currently rises at 36 with 8 new referrals in Jan.)
2. Many declined or rarely attended virtual Early Intervention supports, skipped medical wellness visits including dentistry during the pandemic.
3. Increase in parent report of primary concerns with behavioral components.
4. Given the current timeframe, we are NOT seeing marked progress with an influx in discharges (no longer eligible due to more typical standard scores). We are seeing progress and we have continued to see progress through the pandemic (which at times surprised me) but the levels of improvement are not as remarkable or typical as years past.
5. Typical communication, fine/gross motor and even cognitive delays are still present but the comorbidity of exceptional delays in social/pragmatic and ultimately, behavioral skills combined make measured learning and ultimately IEP progress at a slower rate. Social/pragmatic delays are interfering with overall progress.
6. Parent involvement, participation, enthusiasm and grit appear markedly depressed. Educational teams walk a fine line between empathy, compassion and expecting parents and care givers to step in and "do hard things" in difficult times. The teams are using external motivators such as pizza cards to motivate parents to attempt, complete and turn in 2x monthly parent based home practice pages.
7. Increased rate of meeting attendance with Virtual options.

Where do we go from here? I agree, measuring student outcomes is critical but supporting the parents (in any evidence based manner) is to me, a critical and crucial element. I thought the kids, once exposed to typical learning/situations and with repetition, our inflated numbers would flatten in a year and they would bounce back into typical ranges but it's the apathetic, tired, depressed parents that are lacking resilience and grit currently. I do think another component that would be most valuable and continues to need funding is Preschool for All (or most).

Thank you to any cohort, parent, professional person interested in this dialogue, for reading my insights.

On 2020-04-24 00:57:17, user Philip Davies wrote:

Well, well well ...

This pre-print would make a good script for an episode of Columbo.

The retrospective analysis, as presented, leads the reader to just one conclusion in a bazaar of many possible conclusions.

I am even starting to have sympathy with D. Raoult and his team. I note his hot tempered response to this paper, where he lists two enormous factors that should be considered when wrestling with the data: the fact that the HCQ and HCQ & AZ cohorts were a sicker crowd (he lists lymphopenia) and that the sickest of the non-HCQ ventilated patients were then given HCQ (plus AZ in most cases) in a desperate last bid only for most to die.

Raoult's point is certainly valid.

We must remember that for most of the study period the use of HCQ was "ex-license" on a compassionate basis only. This means only the sickest patients got it. Remember also that this is a retrospective analysis, therefore observational. It was not run as a therapeutic trial. On the other hand, the use of AZ was already accepted (hence 30% of the non-HCQ cohort got it anyway).... although do be aware that by this time there had been quite a lot of focus on potentially dangerous QT lengthening when HCQ and AZ were used together in very sick patients.

The HCQ cohort was, across all key determinants, the weakest and sickest group (it had the poorest prospects looking at age, ethnicity, smoking status, congestive heart failure, peripheral vascular disease, cerebrovascular disease (strokes),dementia, COPD, Diabetes (with and without complications)! ... and indeed, the HCQ and HCQ & AZ cohorts did have 100% more lymphopenia than the non-HCQ group.

BUT, the big asymmetric issues become obvious when we look at the pre- and post- ventilator numbers.

In terms of patients discharged without needing ventilation, the "victorious" non-HCQ group performs poorer than the 2 treated groups. This despite having a better prognostic baseline. But the results for this group change dramatically (for the better) when we look at the outcomes of ventilation. 25 ventilated patients came from this group.... but 19 of these 25 patients were then started on HCQ or HCQ & AZ after ventilation was started. It is screamingly obvious that these would be the sickest patients in that group: they were given such compassionate drugs in extremis. So having ejected 19 of 25 ventilated patients into the other cohorts, the non-HCQ group only had 3 deaths from its remaining 6 ventilated patients.

The numbers of ventilated patients in the other cohorts (HCQ and HCQ & AZ) were thus substantially inflated with these new super-sick patients, who mostly died.

There really can be no conclusion at all when looking at a study of this nature without knowing much more about individual clinical conditions and guiding principles behind clinician's decision making. It's still possible to make some reasonable assumptions:

If I were Columbo?... I would say the non-HCQ cohort contained patients of extremes, with the best and worst potential. The worst would have been the very frail (malignancy and or congestive heart failure maybe ... see the stats), who probably were earmarked for 'supplemental oxygen' only from the very start. Such patients would not have been suitable for compassionate use of non proven drugs (remember, most of this came before the "emergency use" edict by FDA). This would explain the number of non-ventilated patients who died in this group (they may have been given AZ only, not being a controversial drug, but otherwise they did not get any significant interventional therapy). These patients would have had significant chronic disease and very poor obs/indices (including lymphopenia). But given that this cohort had, overall, a better starting prognosis than the other two groups, it means that the remaining patients in the group were promising candidates for survival (with better obs/indices). Such patients, not being part of a clinical trial, would not have been offered HCQ on a compassionate basis unless they got dramatically worse .... and of course, the ones who did get worse on the ventilator were started on HCQ (& often AZ as well) and thus swapped into the HCQ / HCQ & AZ cohorts.

If we can understand that, then we might start to think that in fact HCQ & AZ is the best performing cohort with the other 2 vaguely distant. But this is being unfair to the HCQ cohort:

The reason that a sick patient would be given one experimental drug on a compassionate basis (HCQ) but not have a rather less experimental drug further added (AZ), can really only be explained by considering risk versus benefit. A clinician would choose to use HCQ because the patient was particularly sick. The clinician would only add AZ if it was felt that this was worth the risk.... but a particularly sick patient with significant cardiovascular disease (the HCQ contained the most CVD risk) might then die of a more abrupt arrhythmia through adding yet another QT lengthening drug. I dare say the clinicians were tempted to make some "Hail Mary" plays, but we must remember, these patients were not part of an ongoing trial, these drugs were "ex-license" for compassionate use only and clinicians were still accountable for responsible actions. So for those particularly sick frail patients, it wasn't worth the risk.

I am pretty sure that the HCQ cohort (which had pretty good pre-ventilator stats) crashed badly because it was loaded with the sickest patients .... patients that were too sick to risk adding AZ.

So, the findings of this retrospective analysis are, in my opinion, likely to be incorrect.

I believe I can confidently state that:

1. The HCQ cohort started with the sickest patients and had even more of the sickest added during ventilation. Some were too sick to risk the addition of AZ to existing HCQ.
2. The HCQ/AZ cohort also had some very sick patients (again with more additions during ventilation).
3. The Non-HCQ cohort had the best prognosis overall from the very start (although likely a polarized mixture of the most frail and the most promising)... and then its stats got even better when it jettisoned its sickest ventilated patients into the other 2 cohorts.

It is almost impossible to reach a conclusion from all this. BUT, the most likely finding is NOT that adding HCQ delivers a worse outcome than standard treatment. In fact, if we look at the pre-ventilator stats, the addition of HCQ might actually have provided considerable benefit to a particularly sick group of patients. Whether or not the addition of AZ to HCQ adds benefit is also unclear ... although my 'swingometer' is pointing slightly more to benefit than harm.

Once again. I suggest that a robust study into prophylaxis and early treatment (using sensible safer doses adjusted for pulmonary sequestration) will deliver the most interesting results for CQ/HCQ.

Dr Phil Davies<br /> Aldershot Centre For Health<br /> http://thevirus.uk

On 2020-04-24 09:57:00, user Philip Davies wrote:

Well, well well,

This pre-print would make a good script for an episode of Columbo.

The retrospective analysis, as presented, leads the reader to just one conclusion in a bazaar of many possible conclusions.

I am even starting to have sympathy with D. Raoult and his team. I note his hot tempered response to this paper, where he lists two enormous factors that should be considered when wrestling with the data: the fact that the HCQ and HCQ & AZ cohorts were a sicker crowd (he lists lymphopenia) and that the sickest of the non-HCQ ventilated patients were then given HCQ (plus AZ in most cases) in a desperate last bid only for most to die.

Raoult's point is certainly valid.

We must remember that for most of the study period the use of HCQ was "ex-license" on a compassionate basis only. This means only the sickest patients got it. Remember also that this is a retrospective analysis, therefore observational. It was not run as a therapeutic trial. On the other hand, the use of AZ was already accepted (hence 30% of the non-HCQ cohort got it anyway).... although do be aware that by this time there had been quite a lot of focus on potentially dangerous QT lengthening when HCQ and AZ were used together in very sick patients.

The HCQ cohort was, across all key determinants, the weakest and sickest group (it had the poorest prospects looking at age, ethnicity, smoking status, congestive heart failure, peripheral vascular disease, cerebrovascular disease (strokes),dementia, COPD, Diabetes (with and without complications)! ... and indeed, the HCQ and HCQ & AZ cohorts did have 100% more lymphopenia than the non-HCQ group.

BUT, the big asymmetric issues become obvious when we look at the pre- and post- ventilator numbers.

In terms of patients discharged without needing ventilation, the "victorious" non-HCQ group performs poorer than the 2 treated groups. This despite having a better prognostic baseline. But the results for this group change dramatically (for the better) when we look at the outcomes of ventilation. 25 ventilated patients came from this group.... but 19 of these 25 patients were then started on HCQ or HCQ & AZ after ventilation was started. It is screamingly obvious that these would be the sickest patients in that group: they were given such compassionate drugs in extremis. So having ejected 19 of 25 ventilated patients into the other cohorts, the non-HCQ group only had 3 deaths from its remaining 6 ventilated patients.

The numbers of ventilated patients in the other cohorts (HCQ and HCQ & AZ) were thus substantially inflated with these new super-sick patients, who mostly died.

There really can be no conclusion at all when looking at a study of this nature without knowing much more about individual clinical conditions and guiding principles behind clinician's decision making. It's still possible to make some reasonable assumptions:

If I were Columbo?... I would say the non-HCQ cohort contained patients of extremes, with the best and worst potential. The worst would have been the very frail (malignancy and or congestive heart failure maybe ... see the stats), who probably were earmarked for 'supplemental oxygen' only from the very start. Such patients would not have been suitable for compassionate use of non proven drugs (remember, most of this came before the "emergency use" edict by FDA). This would explain the number of non-ventilated patients who died in this group (they may have been given AZ only, not being a controversial drug, but otherwise they did not get any significant interventional therapy). These patients would have had significant chronic disease and very poor obs/indices (including lymphopenia). But given that this cohort had, overall, a better starting prognosis than the other two groups, it means that the remaining patients in the group were promising candidates for survival (with better obs/indices). Such patients, not being part of a clinical trial, would not have been offered HCQ on a compassionate basis unless they got dramatically worse .... and of course, the ones who did get worse on the ventilator were started on HCQ (& often AZ as well) and thus swapped into the HCQ / HCQ & AZ cohorts.

If we can understand that, then we might start to think that in fact HCQ & AZ is the best performing cohort with the other 2 vaguely distant. But this is being unfair to the HCQ cohort:

The reason that a sick patient would be given one experimental drug on a compassionate basis (HCQ) but not have a rather less experimental drug further added (AZ), can really only be explained by considering risk versus benefit. A clinician would choose to use HCQ because the patient was particularly sick. The clinician would only add AZ if it was felt that this was worth the risk.... but a particularly sick patient with significant cardiovascular disease (the HCQ contained the most CVD risk) might then die of a more abrupt arrhythmia through adding yet another QT lengthening drug. I dare say the clinicians were tempted to make some "Hail Mary" plays, but we must remember, these patients were not part of an ongoing trial, these drugs were "ex-license" for compassionate use only and clinicians were still accountable for responsible actions. So for those particularly sick frail patients, it wasn't worth the risk.

I am pretty sure that the HCQ cohort (which had pretty good pre-ventilator stats) crashed badly because it was loaded with the sickest patients .... patients that were too sick to risk adding AZ.

So, the findings of this retrospective analysis are, in my opinion, likely to be incorrect.

I believe I can confidently state that:

1. The HCQ cohort started with the sickest patients and had even more of the sickest added during ventilation. Some were too sick to risk the addition of AZ to existing HCQ.
2. The HCQ/AZ cohort also had some very sick patients (again with more additions during ventilation).
3. The Non-HCQ cohort had the best prognosis overall from the very start (although likely a polarized mixture of the most frail and the most promising)... and then its stats got even better when it jettisoned its sickest ventilated patients into the other 2 cohorts.

It is almost impossible to reach a conclusion from all this. BUT, the most likely finding is NOT that adding HCQ delivers a worse outcome than standard treatment. In fact, if we look at the pre-ventilator stats, the addition of HCQ might actually have provided considerable benefit to a particularly sick group of patients. Whether or not the addition of AZ to HCQ adds benefit is also unclear ... although my 'swingometer' is pointing slightly more to benefit than harm.

Once again. I suggest that a robust study into prophylaxis and early treatment (using sensible safer doses adjusted for pulmonary sequestration) will deliver the most interesting results for CQ/HCQ.

Dr Phil Davies<br /> Aldershot Centre For Health<br /> http://thevirus.uk

EditView in discussion<br /> Discussion on medrxiv 3 comments<br /> medrxiv viewer<br /> Philip Davies<br /> Philip Davies 4 days ago<br /> The low dose arm of this study is worth following.

The big problem for this study is comparison. It really has not defined the control population at all. The Italian and Chinese references are entirely different. Even the 2 Chinese populations referenced had massively different outcomes because the populations examined were different.

The Italian mortality rate was actually similar to the overall study average here (but much higher than the low dose arm). The Chinese study involved all patients admitted to the two hospitals ... that included a majority of patients with moderate ("ordinary" as the Chinese class it) disease severity. The patients in this Brazilian study were regarded as severe or critical ... such patients (looking at worldwide stats) would attract a mortality of 30-40% plus.

This is the most important factor. Do not compare apples with pears. So far this study points the "swingometer" in favor of benefit versus harm for the use of HQN in patients with advanced disease.

Once again however, we are looking at the potential impact of an orally administered drug to patients with advanced disease. That's a big ask.

For CQ and HCQ the most interesting results will likely come from studies looking at prophylaxis and early treatment (using safe doses, not silly high doses with added drugs that also lengthen QT). We can't yet guess how they will pan out.

Dr Philip Davies<br /> GP<br /> Aldershot Centre For Health, UK<br /> http://thevirus.uk

On 2020-04-16 12:20:10, user Marlowe Fox wrote:

The tests on the efficacy of HCQ are confounded by multiple variables, including comorbidities, symptom onset, prescription drugs (RAAS inhibitors appear to play a key role in viral intensity), and testosterone/estrogen level, to name only a few.

Geneticists, epidemiologists, and other scientists have long used casual diagrams to clearly show variables that may potentially confound their results (1). The Wuhan study at the very least would need to account for the following:

HCQ <— comorbidities —> recovery<br /> HCQ <— symptom onset —> recovery<br /> HCQ <— drug prescriptions —> recovery

Adjusting for the confounding variable would essentially smooth out the flow of information between the treatment (HCQ) and the outcome (recovery), allowing for the inference of causal effects.

Assuming observable data is not available to adjust for confounding variables, a casual mechanism (mediator) could smooth out the flow of information from the treatment to the outcome (so long as the mediator is not influenced by confounder).

Luckily, multiple in vitro studies have been performed. One study posits that HCQ lowers endosomal pH which ultimately inhibits COVID from binding to ACE 2 and decreasing viral intensity (3).

HCQ —> endosomal pH —>glycosylation of COVID cellular receptor —> ACE 2 binding —> viral intensity —> acute lung injury

Another in-silico study posits that HCQ blocks specific protein sites on the host ACE2 cell, thereby thwarting its attempt to infect it and preventing the cytokine storm (over-reaction of the lymphatic system) that some posit is responsible for Acute Lung Injury (3). So here we have an entirely different causal mechanism:

HCQ —> BRD-2 receptor sites —> cytokine storm —> acute lung injury

Despite these problems, some believe that the p-values obviate the need to control for potentially lurking variables. However, they are subject to myriad influences, known as p-hacking. Whether it is the number of tests performed or the number of comparisons made, it increases the chance of finding a statistically significant p-value (4). Three professional statisticians co-authored a paper reviewing the validity of the Wuhan study (5). There were several issues with the data upon which the two significant p-values were based.

I suppose there is also a pragmatic argument: The p-values, along with existing studies and reports, are sufficient enough evidence to offset any concern for lurking variables in these urgent times. In other words, how much evidence is sufficient to warrant large scale roll-out of a low-cost treatment that may have a beneficial effect, from saving individuals who would have otherwise died to curbing its spread?

The consequences of large roll-out: manufacturing, scaling, distribution chains, and so forth could result in a tremendous diversion of resources. How many pharmaceutical manufacturers even have the capacity to roll out production of this magnitude? What if they all start scaling their labor to produce this particular drug. You can’t just put this genie back into the bottle. Not to mention the scientific energy/intellectual capital that would go to proving or disproving this proposed treatment. And why? Because scientific evidence demanded it? No because a tortured p-value and unpublished/unsubstantiated anecdotal evidence caught the attention of some in the media, and it has been over-popularized as a panacea. What about the risk that HCQ is not an effective treatment despite large investments in cash and resources that have been invested? Do you think the wheels of capitalism turn so easily? Investors will want a return and if that means continually touting an ineffective drug through spurious science, they will continue to do so. What about individuals taking HCQ as a prophylactic, believing themselves to be protected against COVID? Or COVID+ individuals taking HCQ and believing themselves to be cured? Or individuals who think: Well, if I get it—I’ll just take HCQ and be fine. This would increase the spread of COVID. From my perspective, the ignorance to viral transmission and the required precautions is widespread. This is just one more reason not to acquiesce to the new social norms of wearing face masks, social distancing, and abiding by shelter-in-place rules. Here, I think an understanding of cognitive psychology is important to anticipate the future behavior of a society in which a cheap and easy-to-manufacture cure is published in the media.

To sum up, HCQ's efficacy is not sufficiently proven to warrant a widespread roll-out, because it could result in several downstream consequences, from the diversion of resources (both manufacturing capabilities and intellectual capital) to increasing the risk threshold of individuals--who spurious believe in an easy and cheap treatment--thereby increasing the infection rate. One of two things needs to happen. Clinical trials that properly adjust for all potential comorbidities. Or the discovery of a causal mechanism (in vivo), which would obviate the need to control/adjust for confounders. For me, this would tip the utilitarian scales in regard to the potential benefits versus the risks.

References

1. Judea Pearl and Dana Mackenzie. 2018. The Book of Why: The New Science of Cause and Effect (1st. ed.). Basic Books, Inc., USA.
2. https://www.ncbi.nlm.nih.go...
3. https://papers.ssrn.com/sol...
4. https://www.scientificameri....
5. https://zenodo.org/record/3....

On 2020-05-15 01:01:11, user Timeisrelative wrote:

This is not my field of study but I hope my comments are helpful to you. Thank you for publishing this important work.

The name "SD" for your metric is confusing for three reasons. 1) Standard deviation which is also used in the paper is commonly abbreviated as SD. 2)Recently less travel has *increased* what people commonly refer to as "social distancing", however your metric "SD" tends to *decrease*. 3)Mobility is only one aspect of the common definition of social distancing. Other aspects are not attending mass gatherings, standing at least 6 ft apart, not shaking hands, etc.(https://hub.jhu.edu/2020/03... "https://hub.jhu.edu/2020/03/13/what-is-social-distancing/)") These other aspects are not captured by your metric so again I think it's confusing to call it a "social distancing ratio" and use the abbreviation SD. Better names might be "Mobility Reduction" or "Relative Mobility".

Further, according to Wikipedia: "During the COVID-19 pandemic, the World Health Organization (WHO) suggested favoring the term "physical distancing" as opposed to "social distancing", in keeping with the fact that it is a physical distance which prevents transmission; people can remain socially connected via technology." (https://en.wikipedia.org/wi... "https://en.wikipedia.org/wiki/Social_distancing)")

Your metric SD is based on "the assumption that when individuals make fewer trips, they physically interact less." But you are not looking at the number of trips directly, instead you look at the deviation from normal levels of trips. Why not look directly at the number of trips? Different areas my have widely varying baseline numbers of trips and one would expect infection rates to vary correspondingly. By measuring the correlation between the actual number of trips and infection rates we could see if that is in fact true.

I'm having trouble understanding the calculation of GR. You state "A GR equal to zero indicates no new confirmed cases were reported in the last three days" However, plugging 0 into the all three Cj in the numerator of the GR calculation leads to log(0/3+0/3+0/3). The result is undefined(negative infinity) not zero. You also state " a value below one means that the growth rate during the last three days is lower than that of the last week" and testing some sample data does not produce this result. Perhaps I'm misinterpreting your formula?

FIG 3 What is the "Raw Date" line? In your description of GR you say "We use 3-day moving averages to smooth volatile case reporting data." Does that statement refer to the 3-day summation in the numerator of "GR" or is there an additional 3-day moving average taken after GR is computed?

The GR calculation itself introduces a lag due to averaging the previous 3 days of data in the numerator and previous 7 days of data in the denominator. This distinction is important as you state that the value of the 9-12 day lag "reflects the time it takes for symptoms to manifest after infection, worsen, and be reported." In fact the lag from the calculation itself is also a factor.

It's also unclear if your source data is the date a positive test was taken or the date the lab results came back. When we are talking about a lag on the order of 10 days, a 1-3 day delay for results could be significant. Further, source data including the date of symptom onset is available in some states and would be more useful as it would eliminate part of the lag which could be affected by test availability and speed.

Why are only the top 25 counties are analyzed? I would be interested in seeing the metrics calculated in other lesser affected areas. In other words, could mobility reductions result in the prevention of outbreaks or just in the reduction of major outbreaks?

The metrics you've chosen (SD and GR) follow very similar paths among all 25 counties analyzed. All 25 counties saw sharp drops in SD between March 10th and March 20th. All 25 counties saw sharp drops in GR a few weeks later. However, adding counties that didn't have a sharp reduction in SD during that time period would be revealing. Also adding counties that had GR paths that either dropped over different time periods or that grew much slower and steadier would also help reveal if GR and SD are correlated in wider situations.

Caption to Fig 2 has redundant text "(vertical dashed red lines)"

"King County, Washington is excluded because it precedes widespread social distancing and was driven by an infection source that differs from other outbreaks in the US." Previously you demonstrated that the SD metric is not well correlated with dates of implementation for local and state social distancing directives. King County shouldn't be excluded just because it precedes widespread social distancing. Also how is it known that the "infection source" is different from the outbreaks at the top 25 counties chosen?

"Last, the data used in this analysis does not differentiate amongst sociodemographic groups, and therefore may not representatively capture all groups such as the elderly, low income families and underrepresentative minorities, for whom social distancing may not be an option, or may not have cell phones." Everyone in those groups with a mobile phone and that has the apps and permissions required for teralytics to track them is expected to be included in the dataset. The dataset may not be representative of the population at large but that is not *because* the dataset doesn't differentiate between sociodemographic groups.

Conclusions: "In conclusion, our results strongly support the conclusion that social distancing pays dividends in the vital reduction of load on hospital systems in the United States." I think this conclusion is too broad. You show no data on load of hospital systems. Your data is on the reduction in reported cases correlating to reduced number of trips in severely affected areas not social distancing as a whole.

On 2020-11-26 12:13:59, user Dr Gareth Davies (Gruff) wrote:

Thank you for this fascinating analysis! It brings together a great deal of very useful information, and the data were presented in useful and transparent ways, and the tables and graphs especially helpful in understanding the data.

I would like to offer some constructive feedback concerning the statistics and their interpretation, as some results appear to have been misinterpreted and this undermines this excellent work.

The use of term "statistically significant" (18 occurrences included negatives) is especially concerning and goes against best-practice. P values and confidence intervals are frequently misinterpreted by both review authors and readers. A lack of evidence is not evidence of lack of effect. This is especially concerning where interpretations of dose, frequency and trial length are interpreted, as they give the impression that some were demonstrably effective whereas others were demonstrably not effective and the latter is not something this study could ascertain and should definitely not conclude or discuss.

(Best practice recommendations from Cochrane Handbook for Systematic Reviews of Interventions version 6.1 C.15.3.2: "Review authors should not describe results as ‘statistically significant’, ‘not statistically significant’ or ‘non-significant’ or unduly rely on thresholds for P values, but report the confidence interval together with the exact P value.")

There is a great deal of heterogeneity in the studies that cannot be measured by an I-squared metric but are important and will affect. Differences in study populations, sizes, country, latitude, age ranges, comorbidities, length of trial, method of assessing outcome, dosing freqency, % participants <25nmol/L, year of study etc. can all introduce very large unmeasurable confounding bias that may strongly influence results in ways that cannot be accounted for by software calculating CIs, P values, or I^2 measures. I would strongly urge great caution in interpreting these as meaningful.

For example, in the group of studies where dose equivalent > 2000 IU/d, the studies vary enormously in almost every attribute and yet the I-squared metric suggests only moderate heterogeneity which is very misleading. It is especially telling that in some studies the reported incidence of > 1 ARI in the intervention and control arms is wildly different across studies: ~17% (Rake 2020) ~74% (Camargo 2020); ~96% (Murdoch 2012), casting strong doubt on the reliability of the measure to capture the outcome of interest to the study.

Berman 2012 showed a small population (N=124) of patients in Sweden (latitude 60°N) susceptible to ARIs (assessed with symptoms, range 40%-60%) and with measured high-prevalence of D deficiency (11.45%) responded positively to >2,000 IU with an odds ratio of 0.43 (CI 0.21 - .88). Among others, these results are combined with Camargo 2020 in New Zealand (40°S) in a very large population (N=5,056) of healthy adults with low prevalence of D deficiency (1.8%) where (ARIs self-reported cold/flu incidence ~75%) with an odds ratio 0.90 to 1.16; and Lehouck 2012 (adults with chronic obstructive lung disease).

It's hard to see how the data from these trials can be meaningfully combined. It's no surprise the comined CI was large 0.84 to 1.31 (in truth it will be far larger since bias and measurement errors have not been accounted for), but the only interpretation possible here is that we cannot interpret anything from these combined data and more research is needed.

The same problem occurs when combining individuals with deficiency (<25nmol/L) giving a combined CI of 0.53 - 1.16. This is reported as "a statistically significant protective effect of vitamin D was not seen in those with the lowest 25(OH)D concentrations" which is then wrongly interpreted to mean evidence of no effect which is simply not the case. All this means is the statistical power was too low to detect an effect with high confidence. Arguably, there IS a detectable effect if we use a lower confidence threshold. (I'm not suggesting this, I'm merely pointing out how careful we need to be interpreting statistics).

Results with CIs crossing null can say nothing about the existence or non-existence of an effect and should not be reported or interpreted as such, especially if the ranges are large. The inability to reject the null hypothesis is not proof of the null hypothesis. It's just lack of study power.

Statements such as "Greater protective efficacy of lower vs higher doses" has no evidential basis and should be removed. This analysis did not show a greater protective effect at lower doses! It showed an effect at lower doses and had insufficient data at higher doses to investigate the question. The subsequent musing over potential mechanisms to explain this imagined difference should also be removed.

I would also strongly caution against multivariable meta-regressions on trial characteristics. There are simply too many potential unmeasured confounders and sources of measurement error to trust that this method will produce meaningful adjustments. There's no telling if this would properly adjust, or conversely introduce bias and loss of precision.

I think if these issues were addressed the study contributes some very important and useful results confirming the positive beneficial effects of vitamin D, and suggests more research could help to answer the questions where the data were insufficient to cast light.

Congratulations on the paper and I hope this feedback is helpful!

Best wishes,

Gareth

On 2020-10-07 06:13:12, user Markku Peltonen wrote:

There were a number of comments on this manuscript on twitter early August, with concerns on errors in the calculations among others. Might be useful for others, so here is what I tweeted on August 5th 2020 (https://twitter.com/MarkkuP...: "https://twitter.com/MarkkuPeltonen/status/1290754970292281349):")

Recently there was a meta-analysis on the effects of masks conducted in Finland. A number of comments has been made about the quality of the piece, so I had a quick look at it. As the analysis was also mentioned at least in Sweden, few quick comments in English. 1/10

Background: the Finnish Ministry of Social Affairs and Health did a systematic review in May 2020 on the use of community face coverings to prevent the spread of Covid-19. There was no meta-analysis in the review, which focused on effectiveness. 2/10

The conclusion on that report was “very little research data available on the effectiveness of community face coverings in preventing the spread of COVID-19 in society.” and evidence “minor” or “non-existent”. 3/10

So, now then a formal meta-analysis, identifying the same 5 randomised controlled trials, showing an effect with relative risk estimate 0.61 (95% CI 0.39-0.96).<br /> Few points: 4/10

The meta-analysis focuses on efficacy; what is achievable potentially when perfect conditions. They do something which they call “account of bias caused by non-compliance”; ie. if persons in the mask-group did not were masks they “adjust” for this. 5/10

To me, this sounds quite controversial: In my world we look at intention-to-treat first, and then perhaps maybe on the “per-protocol”/“as treated”. <br /> Efficacy important, but this is now something different than what the original systematic review aimed at. 6/10

The problems of this accentuate in the Discussion, where the authors do not seem to understand the difference in efficacy and effectiveness, nor the fact that they are actually analysing something else than the original review, and making way too far-fetched conclusions. 7/10

There are other peculiarities, for example “Four of the analyzed studies evaluated the use of masks on respiratory infections directly, and in one the primary outcome was compliance with mask use.”. Hopefully an error, I don’t believe they actually mix the outcomes like this. 8/

. @jejkarppinen added the following comments after my initial post, which I agree with:<br /> - The potential biases in the original papers were not covered.<br /> - Quality of evidence was not evaluated at all.<br /> - Dissemination of the results did not consider the potential problems. 9/10

Finally:<br /> - I've not read the original 5 studies. <br /> - I’m not an expert on systematic reviews/meta-analyses. <br /> - I do think recommendation for masks is motivated, and the evidence is there (but not here..).<br /> - I do think we should be objective when evaluating evidence. 10/10

The original systematic review the Finnish Ministry of Social Affairs and Health in Finnish is here (english abstract only):<br /> http://julkaisut.valtioneuv...

Ps. Somebody noted the lack of preregistered protocol, which reminded me that the PRISMA-guidelines helpful when reporting systematic reviews and meta-analyses. <br /> Their checklist should be followed in reporting:<br /> http://prisma-statement.org

In addition, it was noted by Jesper Kivelä that there are errors in the calculations, these should be corrected (in Finnish):<br /> https://twitter.com/JesperK...

On 2020-10-22 18:25:28, user helen colhoun wrote:

From Helen M Colhoun, AXA Chair in Medical Informatics & Epidemiology, University of Edinburgh. Honorary Consultant in Public Health Medicine.<br /> David McAllister, Senior Clinical Lecturer in Epidemiology and Honorary Consultant in Public Health Medicine, University of Glasgow.<br /> The authors should be commended on attempting to characterise long-COVID-19. Post-viral syndromes are a well- recognised phenomenon and it is important to accurately quantify the full range of the COVID-19 on health. The authors are careful to state that their reported risks pertain only to those with symptomatic COVID. However there are several reasons to think that even among those symptomatic that these results may be subject to serious bias. First of all there is a fundamental weakness of estimating risk based on a non-representative sampling frame, i.e. those who have chosen to use the app in the first place. Then after dropping around half of the 45839 persons who tested positive as being asymptomatic (the numbers in the first part of the flow diagram do not quite add up) a further 14443 are dropped because of starting to use the app whilst already unhealthy- it is not clear whether some of this represents people reporting symptoms well before diagnosis. Then 25% of those remaining are dropped for not persistently logging their symptoms (which could easily be much more common in people with no persisting symptoms than those without). <br /> Another major problem is the lack of specificity of the diagnosis. The disease state of long-COVID19 would appear to be defined as having “at least one symptom lasting more than one day” which has then been further categorised as LC28 or LC56 if symptoms persisted for these number of days. These symptoms include clearly non-specific symptoms such as “fatigue” , “unusual muscle aches and pains” and “skipping a meal”. No comment is made as to the prevalence of such symptoms in the other millions of users of the ZOE app. In the paper we find a hint of the lack of specificity in that in a matched set of test negatives we find that “Individuals with long-COVID were more likely to report relapses (16.0%)….In comparison, in the matched group of 139 SARS-CoV2 negative tested individuals, a new bout of illness was reported in 11.5% of cases.” This difference could easily be attributable to recall bias since at least a large proportion of those with positive tests will have known their result.<br /> Unfortunately this paper is being widely reported in the press as showing that “long COVID affects around 10% of 18 to 49-year-olds who catch the virus.” However those studied comprise just 15% of all those with evidence of infection and it is plausible that many of those not studied have no evidence of long COVID. That is even before we consider the problem that most people who have “caught the virus” don’t even get tested. It would be more correct to say this; “having excluded 85% of people with detected COVID-19 who were asymptomatic or did not continue to record their symptom status, we find that 10% of young people with a positive test report at least one symptom for 28 days and 2% report at least one symptom for 56 days.These symptoms are not specific for COVID-19 and are commonly found in the general population. “ We suggest that the authors to make this important distinction clear in the title of the final version of their manuscript or it will continue to be misquoted. We also suggest that they discuss the impact of the potential biases raised above more fully.

On 2019-07-16 13:28:54, user Guyguy wrote:

EVOLUTION OF THE EBOLA EPIDEMIC IN THE PROVINCES OF NORTH KIVU AND

ITURI.