Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary: 

Cruz-González and colleagues draw on DNA methylation and paired genetic data from 621 participants (n=308 controls; n=313 participants with Alzheimer's Disease). The authors generate a panel of epigenetic biomarkers of aging with a primary focus on the Horvath multi-tissue clock. The authors find weaker correlations between predicted epigenetic age and chronological age in subgroups with higher African ancestry than within a subgroup identified as White. The authors then examine genetic variation as a potential source for between-group differences in epigenetic clock performance. The authors draw on a large collection of publicly available methylation quantitative trait loci datasets and find evidence for substantial overlap between clock CpGs located within the Horvath clock and methQTLs. Going further, the authors show that methQTLs that overlap with Horvath clock CpGs show greater allelic variation in African ancestral groups pointing to a potential explanation for poorer clock performance within this group. 

Thank you for this summary.

Strengths:  

This is an interesting dataset and an important research question. The authors cite issues of portability regarding polygenic risk scores as a motivation to examine between-group differences in the performance of a panel of epigenetic clocks. The authors benefit from a diverse cohort of individuals with paired genetic data and focus on a clinical phenotype, Alzheimer's disease, of clear relevance for studies evaluating age-related biomarkers.  

Weaknesses:  

While the authors tackle an important question using a diverse cohort the current manuscript is lacking some detail that may diminish the potential impact of this paper. For example:  

(1) Information on chronological ages across groups should be reported to ensure there are no systematic differences in ages or age ranges between groups (see point below).  

Thank you for pointing out this omission. The age ranges are similar across cohorts. No individuals under 60 were considered, and the average ages per cohort ranged from 72 to 76. Neither average age nor age range was consistently higher or lower in the admixed cohorts for which the clocks had lower performance compared to the White cohort. We will report the age distributions in supplementary material in the revision.

(2) The authors compare correlations between chronological age and epigenetic age in sub-groups within to correlations reported by Horvath (2013). Attempting to draw comparisons between these two datasets is problematic. The current study has a much smaller N (particularly for sub-group analyses) and has a more restricted age range (6090yrs versus 0-100 yrs). Thus, is an alternative explanation simply that any weaker correlations observed in this study are driven by sample size and a restricted age range? Reporting the chronological ages (and ranges) across subgroups in the current study would help in this regard. Similarly, given the lack of association between AD status and epigenetic age (and very small effect in the white group), it may be of interest to examine the correlation between chronological age and epigenetic age in each group including the AD participants: would the between-group differences in correlations between chronological age and epigenetic be altered by increasing the sample size?

Our conclusions about the reduced accuracy of the clocks in admixed individuals are based on comparisons within the MAGENTA cohorts, not on the comparisons to previous reports. We show significantly reduced accuracy on African American and Puerto Rican cohorts in MAGENTA compared to the White MAGENTA cohort. The reviewer is correct that the lower correlation in each of the cohorts compared to those in the Horvath study is due to the older age range of our cohort. Indeed, other studies applying the Horvath clock have seen similar correlations to those observed on the White MAGENTA cohort (Marioni et al., 2015, Horvath 2013, and Shireby et al., 2020). Following the suggestion to increase sample size, we conducted the chronological age vs. epigenetic age correlation analysis with the inclusion of AD cases. The significantly lower performance of the clock on Puerto Ricans and African Americans relative to White individuals remains after including all individuals in each cohort. We will include these results on the full cohorts in MAGENTA in the revision.

(3) The correlation between chronological age and epigenetic age, while helpful is not the most informative estimate of accuracy. Median absolute error (and an analysis of MAE across subgroups) would be a helpful addition.  

We used correlation because this is commonly used to evaluate the performance of epigenetic age clocks, but we agree that direct error quantification provides a complementary perspective. We confirm that the African American and Puerto Rican cohorts have higher error than the White cohort, and we will report these comparisons in the revision.

(4) More information should be provided about how DNAm data were generated. Were samples from each ancestral group randomized across plates/slides to ensure ancestry and batch are not associated? How were batch effects considered? Given the relatively small sample sizes, it would be important to consider the impact of technical variation on measures of epigenetic age used in the current study. The use of principal Component-based versions of these clocks (Higgins Chen et al., 2023; Nature Aging https://doi.org/10.1038/s43587-022-00248-2) may help address concerns such concerns.  

Thank you for pointing out the need for additional context on data generation. All omics data from the MAGENTA study were generated using protocols that aim to minimize technical artifacts and batch effects. We will add detailed protocol information will be detailed in the revision. We also thank the reviewer for their suggestion on applying the principal component clock to account for potential technical variation. We are planning to perform these analyses and include them in the revision.

(5) Marioni et al., (2015) found a very weak cross-sectional association between DNAm Age and cognitive function (r~0.07) in a cohort of >900 participants. Given these effect sizes, I would not interpret the absence of an effect in the current study to reflect issues of portability of epigenetic biomarkers. 

We agree that previous links between DNAm Age and AD/cognitive function have been small in magnitude. For example, the PhenoAge paper (Levine et al., 2018) and a study using the Horvath clock (Levine et al., 2015) found age acceleration of less than a year in AD patients relative to non-demented individuals. These effects have been detected in studies with relatively small sample sizes (e.g., 700 for Levine et al. 2015 and 604 for Levine et al. 2018). Our study is of similar size, but the cohort-specific analyses have lower power. Nonetheless, we replicate the modest, but significant association with AD in the white MAGENTA cohort. We have performed power calculations and find that we have 26% power to detect an effect of this size in the Cubans, 46% for the Peruvians, 66% for the Whites, 74% for the Puerto Ricans, and 84% for the African Americans. Given the relatively high power in the Puerto Rican and African American cohorts, we suggest that the reduced accuracy of the clocks contributes to the lack of association. We will also add caveats about power and the small sample size in the revision.

6) The methQTL analyses presented are suggestive of potential genetic influence on DNAm at some Horvath CpGs. Do authors see differences in DNAm across ancestral groups at these potentially affected CpGs? This seems to be a missing piece together (e.g., estimating the likely impact of methQTL on clock CpG DNAm). 

Thank you for this excellent suggestion. We will add this analysis in the revision. This will enable us to test for further evidence for our hypothesis about the role of ancestryspecific meQTL on clock accuracy.  

Reviewer #2 (Public review):

Summary:  

This paper seeks to characterize the portability of methylation clocks across groups. Methylation clocks are trained to predict biological aging from DNA methylation but have largely been developed in datasets of individuals with primarily European ancestries. Given that genetic variation can influence DNA methylation, the authors hypothesize that methylation clocks might have reduced accuracy in non-European ancestries.  

Strengths:  

The authors evaluate five methylation clocks in 621 individuals from the MAGENTA study. This includes approximately 280 individuals sampled in Puerto Rico, Cuba, and Peru, as well as approximately 200 self-identified African American individuals sampled in the US. To understand how methylation clock accuracy varies with proportion of nonEuropean ancestry, the authors inferred local ancestry for the Puerto Rican, Cuban, Peruvian, and African American cohorts. Overall, this paper presents solid evidence that methylation clocks have reduced accuracy in individuals with non-European ancestries, relative to individuals with primarily European ancestries. This should be of great interest to those researchers who seek to use methylation clocks as predictors of agerelated, late-onset diseases and other health outcomes.

Thank you for this summary.

Weaknesses:  

One clear strength of this paper is the ability to do more sophisticated analyses using the local ancestry calls for the MAGENTA study. It would be valuable to capitalize on this strength and assess portability across the genetic ancestry spectrum, as was recently advocated by Ding et al. in Nature (2023). For example, the authors could regress non-European local ancestry fraction on measures of prediction accuracy. This could paint a clearer picture of the relationship between genetic ancestry and clock accuracy, compared to looking at overall correlations within each cohort. 

Thank you for this excellent suggestion. We agree that modeling portability across genetic ancestry as a spectrum would help support our conclusions. We will add this to the revision.

The authors present two possible reasons that methylation clocks might have reduced accuracy in individuals with non-European ancestries: genetic variants disrupting methylation sites (i.e., "disruptive variants") and genetic variants influencing methylation sites (i.e., meQTLs). The authors conclude disruptive variants do not contribute to poor methylation clock portability, but the evidence in support of this conclusion is incomplete. The site frequency spectrum of disruptive variants in Figure 4 is estimated from all gnomAD individuals, and gnomAD is comprised of primarily European individuals. Thus, the observation that disruptive variants are generally rare in gnomAD does not rule them out as a source of poor clock portability in admixed individuals with non-European ancestries. 

Thank you for this question. The allele frequencies were so low that even if they all occurred in individuals of non-European ancestries, they would still be incredibly rare. Nonetheless, in the revision, we will make this clear by reporting ancestry-specific allele frequencies.

It is also unclear to what extent meQTLs impact methylation clock portability. The authors find that the frequency of meQTLs is higher in African ancestry populations, but this could reflect the fact that some of the analyzed meQTLs were ascertained in African Americans. The number of meQTL-affected methylation sites also varies widely between clocks, ranging from 6 to 271; thus, meQTLs likely impact the portability of different clocks in different ways. Overall, the paper would benefit from a more quantitative assessment of the extent to which meQTLs influence clock portability. 

We agree that the meQTL likely influence the clocks in different ways and that the ascertainment of the meQTLs in different populations makes direct comparisons challenging. To provide mechanistic insights into the ways that meQTL influence the methylation clocks, we plan to leverage the individual-level genetic data generated for the MAGENTA individuals. This will allow us to explore whether the individuals who have the specified clock-influencing meQTL receive less accurate predictions from the methylation clocks. In addition, the new analysis of whether individuals from different cohorts have different methylation levels at clock CpGs with ancestry-variable meQTLs will help establish the differences between groups (see response to Reviewer #1 point 6). Finally, to resolve potential bias due to ascertaining some of the meQTL in African Americans, we will conduct the same analyses from the manuscript, holding out the set of meQTL from African Americans. These results will be included in the revision.

The paper implies that methylation clocks have an inferior ability to predict AD risk in admixed populations relative to white individuals, but the difference between white AD patients and controls is not significant when correcting for multiple testing. This nuance should be made more explicit. 

We agree that the signal is not particularly strong in the white cohort, but the effect size is in line with previous studies. We will add power calculations and discussion to help the interpretation of these results (see response to Reviewer #1 point 5).  

Finally, this paper overlooks the possibility that environmental exposures co-vary with genetic ancestry and play a role in decreasing the accuracy of methylation clocks in genetically admixed individuals. Quantifying the impact of environmental factors is almost certainly outside of the scope of this paper. However, it is worth acknowledging the role of environmental factors to provide the field with a more comprehensive overview of factors influencing methylation clock portability. It is also essential to avoid the assumption that correlations with genetic ancestry necessarily arise from genetic causes.  

We entirely agree about the importance of discussing environmental exposures. We did not intend to discount them in our manuscript. We will clarify their potential role and the scope of our analyses in the revision. We expect that environmental factors certainly contribute to differences between groups. The revisions outlined above may help us better quantify the genetic contribution.

Reviewer #3 (Public review):

This manuscript examines the accuracy of DNA methylation-based epigenetic clocks across multiple cohorts of varying genetic ancestry. The authors find that clocks were generally less accurate at predicting age in cohorts with large proportions of nonEuropean (especially African) ancestry, compared to cohorts with high European ancestry proportions. They suggest that some of this effect might be explained by meQTLs that occur near CpG sites included in clocks, because these variants may be at higher frequencies (or at least different frequencies) in cohorts with high proportions of non-European ancestry relative to the training set. They also provide discussions of potential paths forward to alleviate bias and improve portability for future clock algorithms.  

The topic is timely due to the increasing popularity of DNA methylation-based clocks and the acknowledgment that many algorithms (e.g., polygenic risk scores) lack portability when applied to cohorts that substantially differ in ancestry or other characteristics from the training set. This has been discussed to some degree for DNA methylation-based clocks, but could of course use more discussion and empirical attention which the authors nicely provide using an impressive and diverse collection of data.  

The manuscript is clear and well-written, however, some key background was missing (e.g., what we know already about the ancestry composition of clock training sets) and most importantly several analyses would benefit from being taken one step further. For example, the main argument of the paper is that ancestry impacts clock predictions, but this is determined by subsetting the data by recruitment cohort rather than analyzing ancestry as a continuous variable. Extending some of the analyses could really help the authors nail down their hypothesized sources of lack of portability, which is critical for making recommendations to the community and understanding the best paths forward.  

Thank you for these suggestions. As noted in our response to reviewer #2, we will analyze ancestry as a continuous variable in the revision. We will also add details on the training of previous clocks and previous work on clock accuracy.

Author response:

We thank the reviewers for the careful review of our manuscript. Overall, they were positive about our use of cutting-edge methods to identify six inversions segregating in Lake Malawi. Their distribution in ~100 species of Lake Malawi species demonstrated that they were differentially segregating in different ecogroups/habitats and could potentially play a role in local adaptation, speciation, and sex determination. Reviewers were positive about our finding that the chromosome 10 inversion was associated with sex-determination in a deep benthic species and its potential role in regulating traits under sexual selection. They agree that this work is an important starting point in understanding the role of these inversions in the amazing phenotypic diversity found in the Lake Malawi cichlid flock.

There were two main criticisms that were made which we summarize:

(1) Lack of clarity. It was noted that the writing could be improved to make many technical points clearer. Additionally, certain discussion topics were not included that should be.

We will rewrite the text and add additional figures and tables to address the issues that were brought up in a point-by-point response. We will improve/include (1) the nomenclature to understand the inversions in different lineages, (2) improved descriptions for various genomic approaches, (3) a figure to document the samples and technologies used for each ecogroup, and 4) integration of LR sequences to identify inversion breakpoints to the finest resolution possible.

(2) We overstate the role that selection plays in the spread of these inversions and neglect other evolutionary processes that could be responsible for their spread.

We agree with the overarching point. We did not show that selection is involved in the spread of these inversions and other forces can be at play. Additionally, there were concerns with our model that the inversions introgressed from a Diplotaxodon ancestor into benthic ancestors and incomplete lineage sorting or balancing selection (via sex determination) could be at play. Overall, we agree with the reviewers with the following caveats. 1. Our analysis of the genetic distance between Diplotaxodons and benthic species in the inverted regions is more consistent with their spread through introgression versus incomplete lineage sorting or balancing selection. 2. This question of selection is much more complicated in the context of the Lake Malawi cichlid radiation with ~800 different species. We believe the role of these inversions must be considered in a species- and time-specific way. In other words, the evolutionary forces acting on these inversions at the time of their formation are likely different than the role of the evolutionary forces acting now. Further the role of these inversions is likely different in different species. For example, the inversion of 10 and 11 play a role in sex determination in some species but not others and the potential pressures acting on the inverted and non-inverted haplotypes will be very different. These are very interesting and important questions booth for understanding the adaptive radiations in Lake Malawi and in general, and we are actively studying crosses to understand the role of these inversions in phenotypic variation between two species. We will modify the text to make all of these points clearer.

Author response:

Reviewer #1:

Weaknesses:

(1) The crystal structure of HsIFT172c reveals a single globular domain formed by the last three TPR repeats and C-terminal residues of IFT172. However, the authors subdivide this globular domain into TPR, linker, and U-box-like regions that they treat as separate entities throughout the manuscript. This is potentially misleading as the U-box surface that is proposed to bind ubiquitin or E2 is not surface accessible but instead interacts with the TPR motifs. They justify this approach by speculating that the presented IFT172c structure represents an autoinhibited state and that the U-box-like domain can become accessible following phosphorylation. However, additional evidence supporting the proposed autoinhibited state and the potential accessibility of the U-box surface following phosphorylation is needed, as it is not tested or supported by the current data.

We thank the reviewer for this comment. IFT172C contains TPR region and Ubox-like region which are admittedly tightly bound to each other. While there is a possibility that this region functions and exists as one domain, below are the reasons why we chose to classify these regions as two different domains.

(1) TPR and Ubox-like regions are two different structural classes

(2) TPR region is linked to Ubox-like region via a long linker which seems poised to regulate the relative movement between these regions.

(3) Many ciliopathy mutations are mapped to the interface of TPR region and the Ubox region hinting at a regulatory mechanism governed by this interface.

(2) While in vitro ubiquitination of IFT172 has been demonstrated, in vivo evidence of this process is necessary to support its physiological relevance.

We thank the reviewer for this comment. We are currently working on identifying the substrates of IF172 to reveal the physiological relevant of its ubiquitination activity.

(3) The authors describe IFT172 as being autoubiquitinated. However, the identified E2 enzymes UBCH5A and UBCH5B can both function in E3-independent ubiquitination (as pointed out by the authors) and mediate ubiquitin chain formation in an E3-independent manner in vitro (see ubiquitin chain ladder formation in Figure 3A). In addition, point mutation of known E3-binding sites in UBCH5A or TPR/U-box interface residues in IFT172 has no effect on the mono-ubiquitination of IFT172c1. Together, these data suggest that IFT172 is an E3-independent substrate of UBCH5A in vitro. The authors should state this possibility more clearly and avoid terminology such as "autoubiquitination" as it implies that IFT172 is an E3 ligase, which is misleading. Similarly, statements on page 10 and elsewhere are not supported by the data (e.g. "the low in vitro ubiquitination activity exhibited by IFT172" and "ubiquitin conjugation occurring on HsIFT172C1 in the presence of UBCH5A, possibly in coordination with the IFT172 U-box domain").

We now consider this possibility and tone down our statements about the autoubiquitination activity of IFT172 in a revised version of the manuscript.

(4) Related to the above point, the conclusion on page 11, that mono-ubiquitination of IFT172 is U-box-independent while polyubiquitination of IFT172 is U-box-dependent appears implausible. The authors should consider that UBCH5A is known to form free ubiquitin chains in vitro and structural rearrangements in F1715A/C1725R variants could render additional ubiquitination sites or the monoubiquitinated form of IFT172 inaccessible/unfavorable for further processing by UBCH5A.

We now consider this possibility and tone down our statements about the autoubiquitination activity of IFT172 in the conclusion on pg. 11.

(5) Identification of the specific ubiquitination site(s) within IFT172 would be valuable as it would allow targeted mutation to determine whether the ubiquitination of IFT172 is physiologically relevant. Ubiquitination of the C1 but not the C2 or C3 constructs suggests that the ubiquitination site is located in TPRs ranging from residues 969-1470. Could this region of TPR repeats (lacking the IFT172C3 part) suffice as a substrate for UBCH5A in ubiquitination assays?

We thank the reviewer for raising this important point about ubiquitination site identification. While not included in our manuscript, we did perform mass spectrometry analysis of ubiquitination sites using wild-type IFT172 and several mutants (P1725A, C1727R, and F1715A). As shown in the figure below, we detected multiple ubiquitination sites across these constructs. The wild-type protein showed ubiquitination at positions K1022, K1237, K1271, and K1551, while the mutants displayed slightly different patterns of modification. However, we should note that the MS intensity signals for these ubiquitinated peptides were relatively low compared to unmodified peptides, making it difficult to draw strong conclusions about site specificity or physiological relevance.

Author response image 1.

These results align with the reviewer's suggestion that ubiquitination occurs within the TPR-containing region. However, given the technical limitations of the MS analysis and the potential for E3-independent ubiquitination by UBCH5A, we have taken a conservative approach in interpreting these findings.

(6) The discrepancy between the molecular weight shifts observed in anti-ubiquitin Western blots and Coomassie-stained gels is noteworthy. The authors show the appearance of a mono-ubiquitinated protein of ~108 kDa in anti-ubiquitin Western blots. However, this molecular weight shift is not observed for total IFT172 in the corresponding Coomassie-stained gels (Figures 3B, D, F). Surprisingly, this MW shift is visible in an anti-His Western blot of a ubiquitination assay (Fig 3C). Together, this raises the concern that only a small fraction of IFT172 is being modified with ubiquitin. Quantification of the percentage of ubiquitinated IFT172 in the in vitro experiments could provide helpful context.

We do acknowledge in the manuscript is that the conjugation of ubiquitins to IFT172C is weak (Page 16). Future experiments of identification of potential substrates and its implications in ciliary regulation will provide further context to our in vitro ubiquitination experiments.

(7) The authors propose that IFT172 binds ubiquitin and demonstrate that GST-tagged HsIFT172C2 or HsIFT172C3 can pull down tetra-ubiquitin chains. However, ubiquitin is known to be "sticky" and to have a tendency for weak, nonspecific interactions with exposed hydrophobic surfaces. Given that only a small proportion of the ubiquitin chains bind in the pull-down, specific point mutations that identify the ubiquitin-binding site are required to convincingly show the ubiquitin binding of IFT172.

(8) The authors generated structure-guided mutations based on the predicted Ub-interface and on the TPR/U-box interface and used these for the ubiquitination assays in Fig 3. These same mutations could provide valuable insights into ubiquitin binding assays as they may disrupt or enhance ubiquitin binding (by relieving "autoinhibition"), respectively. Surprisingly, two of these sites are highlighted in the predicted ubiquitin-binding interface (F1715, I1688; Figure 4E) but not analyzed in the accompanying ubiquitin-binding assays in Figure 4.

We agree that these mutations could provide insights into ubiquitin binding by IFT172. We are currently pursuing further mutagenesis studies on the IFT172-Ub interface based on the AF model. We however have evaluated the ubiquitin binding activity of the mutant F1715A using similar pulldowns, which showed no significant impact for the mutation on the ubiquitin binding activity of IFT172. We are yet to evaluate the impact of alternate amino acid substitutions at these positions. The I1688 mutants we cloned could not be expressed in soluble form, thus could not be used for testing in ubiquitination activity or ubiquitin binding assays.

(9) If IFT172 is a ubiquitin-binding protein, it might be expected that the pull-down experiments in Figure S1 would identify ubiquitin, ubiquitinated proteins, or E2 enzymes. These were not observed, raising doubt that IFT172 is a ubiquitin-binding protein.

It is likely that IFT172 only binds ubiquitin with low affinity as indicated by our in vitro pulldowns and the AF interface. In our pull down experiment performed using the Chlamy flagella extracts, we have used extensive washes to remove non-specific interactors. This might have also excluded the identification of weak but bona fide interactors of IFT172. Additionally, we have not used any ubiquitination preserving reagents such as NEM in our pulldown buffers, exposing the cellular ubiquitinated proteins to DUB mediated proteolysis further preventing their identification in our pulldown/MS experiment.

(10) The cell-based experiments demonstrate that the U-box-like region is important for the stability of IFT172 but does not demonstrate that the effect on the TGFb pathway is due to the loss of ubiquitin-binding or ubiquitination activity of IFT172.

We acknowledge that our current data cannot distinguish whether the TGFβ pathway defects arise from general protein instability or from specific loss of ubiquitin-related functions. Our experiments demonstrate that the U-box-like region is required for both IFT172 stability and proper TGFβ signaling, but we agree that establishing a direct mechanistic link between these phenomena would require additional evidence. We will revise our discussion to more clearly acknowledge this limitation in our current understanding of the relationship between IFT172's U-box region and TGFβ pathway regulation.

(11) The challenges in experimentally validating the interaction between IFT172 and the UBX-domain-containing protein are understandable. Alternative approaches, such as using single domains from the UBX protein, implementing solubilizing tags, or disrupting the predicted binding interface in Chlamydomonas flagella pull-downs, could be considered. In this context, the conclusion on page 7 that "The uncharacterized UBX-domain-containing protein was validated by AF-M as a direct IFT172 interactor" is incorrect as a prediction of an interaction interface with AF-M does not validate a direct interaction per se.

We agree with the reviewer that our AlphaFold-Multimer (AF-M) predictions alone do not constitute experimental validation of a direct interaction. We appreciate the reviewer's understanding of the technical challenges in validating this interaction experimentally. We will revise our text to more precisely state that "The uncharacterized UBX-domain-containing protein was validated by AF-M as a potential direct IFT172 interactor" and will discuss the AF-M predictions as computational evidence that suggests, but does not prove, a direct interaction. This more accurately reflects the current state of our understanding of this potential interaction.

Reviewer #3:

Weaknesses:

(1) Interaction studies were carried out by pulldown experiments, which identified more IFT172 interaction partners. Whether these interactions can be seen in living cells remains to be elucidated in subsequent studies.

We agree with the reviewer that validation of protein-protein interactions in living cells provides important physiological context. While our pulldown experiments have identified several promising interaction partners and the AF-M predictions provide computational support for these interactions, we acknowledge that demonstrating these interactions in vivo would strengthen our findings. However, we believe our current biochemical and structural analyses provide valuable insights into the molecular basis of IFT172's interactions, laying important groundwork for future cell-based studies.

(2) The cell culture-based experiments in the IFT172 mutants are exciting and show that the U-box domain is important for protein stability and point towards involvement of the U-box domain in cellular signaling processes. However, the characterization of the generated cell lines falls behind the very rigorous analysis of other aspects of this work.

We thank the reviewer for noting that the characterization of our cell lines could be more rigorous. In the revised manuscript, we will provide additional characterization of the cell lines, including detailed sequencing information and validation data for the IFT172 mutants. This will bring the documentation of our cell-based experiments up to the same standard as other aspects of our work.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The authors tested whether learning to suppress (ignore) salient distractors (e.g., a lone colored nontarget item) via statistical regularities (e.g., the distractor is more likely to appear in one location than any other) was proactive (prior to paying attention to the distractor) or reactive (only after first attending the distractor) in nature. To test between proactive and reactive suppression the authors relied on a recently developed and novel technique designed to "ping" the brain's hidden priority map using EEG inverted encoding models. Essentially, a neutral stimulus is presented to stimulate the brain, resulting in activity on a priority map which can be decoded and used to argue when this stimulation occurred (prior to or after attending to a distracting item). The authors found evidence that despite learning to suppress the high probability distractor location, the suppression was reactive, not proactive in nature.

Overall, the manuscript is well-written, tests a timely question, and provides novel insight into a long-standing debate concerning distractor suppression.

Strengths (in no particular order):

(1) The manuscript is well-written, clear, and concise (especially given the complexities of the method and analyses).

(2) The presentation of the logic and results is mostly clear and relatively easy to digest.

(3) This question concerning whether location-based distractor suppression is proactive or reactive in nature is a timely question.

(4) The use of the novel "pinging" technique is interesting and provides new insight into this particularly thorny debate over the mechanisms of distractor suppression.

Weaknesses (in no particular order):

(1) The authors tend to make overly bold claims without either A) mentioning the opposing claim(s) or B) citing the opposing theoretical positions. Further, the authors have neglected relevant findings regarding this specific debate between proactive and reactive suppression.

(2) The authors should be more careful in setting up the debate by clearly defining the terms, especially proactive and reactive suppression which have recently been defined and were more ambiguously defined here.

(3) There were some methodological choices that should be further justified, such as the choice of stimuli (e.g., sizes, colors, etc.).

(4) The figures are often difficult to process. For example, the time courses are so far zoomed out (i.e., 0, 500, 100 ms with no other tick marks) that it makes it difficult to assess the timing of many of the patterns of data. Also, there is a lot of baseline period noise which complicates the interpretations of the data of interest.

(5) Sometimes the authors fail to connect to the extant literature (e.g., by connecting to the ERP components, such as the N2pc and PD components, used to argue for or against proactive suppression) or when they do, overreach with claims (e.g., arguing suppression is reactive or feature-blind more generally).

We thank the reviewer for their insightful feedback and have made several adjustments to address the concerns raised. To provide a balanced discussion, we tempered our claims about suppression mechanisms and incorporated additional references to opposing theoretical positions, including the signal suppression hypothesis, while clarifying the definitions of proactive and reactive suppression based on recent terminology (Liesefeld et al., 2024). We justified methodological choices, such as the slight size differences between stimuli to achieve perceptual equivalence and the randomization of target and distractor colors to mitigate potential luminance biases. We have revised our figure to enhance figure clarity. Lastly, while our counterbalanced design precluded reliable ERP assessments (e.g., N2pc, PD), we discussed their potential relevance for future research and ensured consistency with the broader literature on suppression mechanisms.

Reviewer #2 (Public Review):

Summary:

The authors investigate the mechanisms supporting learning to suppress distractors at predictable locations, focusing on proactive suppression mechanisms manifesting before the onset of a distractor. They used EEG and inverted encoding models (IEM). The experimental paradigm alternates between a visual search task and a spatial memory task, followed by a placeholder screen acting as a 'ping' stimulus -i.e., a stimulus to reveal how learned distractor suppression affects hidden priority maps. Behaviorally, their results align with the effects of statistical learning on distractor suppression. Contrary to the proactive suppression hypothesis, which predicts reduced memory-specific tuning of neural representations at the expected distractor location, their IEM results indicate increased tuning at the high-probability distractor location following the placeholder and prior to the onset of the search display.

Strengths:

Overall, the manuscript is well-written and clear, and the research question is relevant and timely, given the ongoing debate on the roles of proactive and reactive components in distractor processing. The use of a secondary task and EEG/IEM to provide a direct assessment of hidden priority maps in anticipation of a distractor is, in principle, a clever approach. The study also provides behavioral results supporting prior literature on distractor suppression at high-probability locations.

Weaknesses:

(1) At a conceptual level, I understand the debate and opposing views, but I wonder whether it might be more comprehensive to present also the possibility that both proactive and reactive stages contribute to distractor suppression. For instance, anticipatory mechanisms (proactive) may involve expectations and signals that anticipate the expected distractor features, whereas reactive mechanisms contribute to the suppression and disengagement of attention.

This is an excellent point. Indeed, while many studies, including our own, have tried to dissociate between proactive and reactive mechanisms, as if it is one or the other, the overall picture is arguably more nuanced. We have added a paragraph to the discussion on page 19 to address this. At the same time, (for more details see our responses to your comments 3 and 5), we have added a paragraph where we provide an alternative explanation of the current data in the light of the dual-task nature of our experiment.

(2) The authors focus on hidden priority maps in pre-distractor time windows, arguing that the results challenge a simple proactive view of distractor suppression. However, they do not provide evidence that reactive mechanisms are at play or related to the pinging effects found in the present paradigm. Is there a relationship between the tuning strength of CTF at the high-probability distractor location and the actual ability to suppress the distractor (e.g., behavioral performance)? Is there a relationship between CTF tuning and post-distractor ERP measures of distractor processing? While these may not be the original research questions, they emerge naturally and I believe should be discussed or noted as limitations.

Thank you for raising these important points. While CTF slopes have been shown to provide spatially and temporally resolved tracking of covert spatial attention and memory representations at the group level, to the best of our knowledge, no study to date has found a reliable correlation between CTFs and behavior. Moreover, the predictive value of the learned suppression effect, while also highly reliable at the group level, has been proven to be limited when it comes to individual-level performance (Ivanov et al. 2024; Hedge et al., 2018). Nevertheless, based on your suggestion, we explored whether there was a correlation between the averaged gradient slope within the time window where the placeholder revived the memory representation and the average distance slope in reaction times for the learned suppression effect. This correlation was not significant (r = .236, p = 0.267), which, considering our sample size and the reasons mentioned earlier, is not particularly surprising. Given that our sample size was chosen to measure group level effects, we decided not to include individual differences analysis it in the manuscript.

Regarding the potential link between the CTF tuning profile and post-distractor ERP measures like N2pc and Pd, our experimental design presented a specific challenge. To reliably assess lateralized ERP components like N2pc or Pd the high probability location must be restricted to static lateralized positions (e.g., on the horizontal midline). Our counterbalanced design (see also our response to comment 9 by reviewer 1), which was crucial to avoid bias in spatial encoding models, precluded such a targeted ERP analysis.

(3) How do the authors ensure that the increased tuning (which appears more as a half-split or hemifield effect rather than gradual fine-grained tuning, as shown in Figure 5) is not a byproduct of the dual-task paradigm used, rather than a general characteristic of learned attentional suppression? For example, the additional memory task and the repeated experience with the high-probability distractor at the specific location might have led to longer-lasting and more finely-tuned traces for memory items at that location compared to others.

Thank you for raising these important points. Indeed, a unique aspect of our study that sets it apart from other studies, is that the effects of learned suppression were not measured directly via an index of distractor processing, but rather inferred indirectly via tuning towards a location in memory. The critical assumption here, that we now make explicit on page 18, is that various sources of attentional control jointly determine the priority landscape, and this priority landscape can be read out by neutral ping displays. An alternative however, as suggested by the reviewer, is that memory representations may have been sharper when they remembered location was at the high probability distractor location. We believe this is unlikely for various reasons. First, at the behavioral level there was no evidence that memory performance differed for positions overlapping high and low probability distractor locations (also see our response to reviewer 3 minor comment 4). Second, there was no hint whatsoever that the memory representation already differed during encoding or maintenance (This is now explicitly indicated in the revised manuscript on page 14), which would have been expected if the spatial distractor imbalance modulated the spatial memory representations.

Nevertheless, as discussed in more detail in response to comment 5, there is an alternative explanation for the observed gradient modulation that may be specific to the dual nature of our experiment.

(4) It is unclear how IEM was performed on total vs. evoked power, compared to typical approaches of running it on single trials or pseudo-trials.

Thank you for pointing out that our methods were not clear. We did not run our analysis on single trials because we were interested in separately examining the spatial selectivity of both evoked alpha power (phase locked activity aligned with stimulus onset) and total alpha power (all activity regardless of signal phase). It is only possible to calculate evoked and total power when averaging across trials. Thus, when we partitioned the data into sets for the IEM analysis, we averaged trials for each condition/stimulus location to obtain a measurement of evoked and total power each condition for each set. This is the same approach used in previous work (e.g. Foster et al., 2016; van Moorselaar et al., 2018).

We reviewed our method section and can see why this was unclear. In places, we had incorrectly described the dimensions of training and test data as electrodes x trials. To address this, we’ve rewritten the “Time frequency analysis”, “Inverted encoding model” sections, and added a new “Training and test data” section. We hope that these sections are easier to follow.

(5) Following on point 1. What is the rationale for relating decreased (but not increased) tuning of CTF to proactive suppression? Could it be that proactive suppression requires anticipatory tuning towards the expected feature to implement suppression? In other terms, better 'tuning' does not necessarily imply a higher signal amplitude and could be observable even under signal suppression. The authors should comment on this and clarify.

We appreciate your highlighting of these highly relevant alternative explanations. In response, we have revised a paragraph in the General Discussion on page 18 to explicitly outline our rationale for associating decreased tuning with proactive suppression. However, in doing so, we now also consider the alternative perspective that proactive suppression might actually require enhanced tuning towards the expected feature to implement suppression effectively.

It's important to note that both of these interpretations – decreased tuning as a sign of suppression and increased tuning as a preparatory mechanism for suppression – diverge significantly from the commonly held model (including our own initial assumptions) wherein weights at the to-be-suppressed location are simply downregulated.

Minor:

(1) In the Word file I reviewed, there are minor formatting issues, such as missing spaces, which should be double-checked.

Thank you! We have now reviewed the text thoroughly and tried our best to avoid formatting issues.

(2) Would the authors predict that proactive mechanisms are not involved in other forms of attention learning involving distractor suppression, such as habituation?

Habituation is a form of non-associative learning where the response to a repetitive stimulus decreases over time. As such, we would not characterize these changes as “proactive”, as it only occurs following the (repeated) exposure to the stimulus. 

(3) A clear description in the Methods section of how individual CTFs for each location were derived would help in understanding the procedure.

Thank you. We have now added several sentences on page 27 to clarify how individual CTFs in Figure 3 and distance CTFs in Figure 5 are calculated.

“The derived channel responses (8 channels × 8 location bins) were then used for the following analyses: (a) calculating individual Channel Tuning Functions (CTFs) based on each of the eight physical location bins (e.g., Figure 3C and 3D); (b) grouping responses according to the distance between each physical location and the high-probability distractor location to calculate distance CTFs (e.g., Figure 5); and (c) averaging across location bins to represent the general strength of spatial selectivity in tracking the memory cue, irrespective of its specific location (e.g., Figure 3A and 3B).”

(4) Why specifically 1024 resampling iterations?

Thank you for your question. The statistical analysis was conducted using the permutation_cluster_1samp_test function within the MNE package in Python. We have clarified this on page 25. The choice of 1024 permutations reflects the default setting of the function, which is generally considered sufficient for robust non-parametric statistical testing. This number provides a balance between computational efficiency and the precision of p-value estimation in the context of our analyses.

Reviewer #3 (Public Review):

Summary:

In this experiment, the authors use a probe method along with time-frequency analyses to ascertain the attentional priority map prior to a visual search display in which one location is more likely to contain a salient distractor.  The main finding is that neural responses to the probe indicate that the high probability location is attended, rather than suppressed, prior to the search display onset.  The authors conclude that suppression of distractors at high-probability locations is a result of reactive, rather than proactive, suppression.

Strengths:

This was a creative approach to a difficult and important question about attention.  The use of this "pinging" method to assess the attentional priority map has a lot of potential value for a number of questions related to attention and visual search. Here as well, the authors have used it to address a question about distractor suppression that has been the subject of competing theories for many years in the field. The paper is well-written, and the authors have done a good job placing their data in the larger context of recent findings in the field.

Weaknesses:

The link between the memory task and the search task could be explored in greater detail. For example, how might attentional priority maps change because of the need to hold a location in working memory? This might limit the generalizability of these findings. There could be more analysis of behavioral data to address this question. In addition, the authors could explore the role that intertrial repetition plays in the attentional priority map as these factors necessarily differ between conditions in the current design. Finally, the explanation of the CTF analyses in the results could be written more clearly for readers who are less familiar with this specific approach (which has not been used in this field much previously).

We appreciate the reviewer's valuable feedback and have made significant revisions to address the concerns raised. To clarify the connection between the memory and search tasks, we conducted additional analyses to explore the effects of spatial distance between the memory cue location and the high-probability distractor location on behavioral performance. We also investigated the potential influence of intertrial repetition effects on the observed results by removing trials with location repetitions. To enhance clarity, we revised the explanation of the CTF analyses in the Results section and improved figure annotations to ensure accessibility for readers unfamiliar with this approach. Collectively, these updates further discuss how the pattern of CTF slopes reflect the interplay between memory and search tasks while addressing key methodological and interpretative considerations.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Suggestions/Critiques (in no particular order)

(1) The authors discuss the tripartite model (bottom-up, top-down, and selection history) but neglect recent and important discussions of why this trichotomy might be unnecessarily complicated (e.g., Anderson, 2024: Trichotomy revisited: A monolithic theory of attentional control). Simply put, one of the 3 pillars (i.e., selection history) likely does not fall into a unitary construct or "box"; instead, it likely contains many subcomponents (e.g., reward associations, stimulus-response habit learning, statistical learning, etc.). Since the focus of the current study is learned distractor suppression based on the statistical regularities of the distractor, the authors should comment on which aspects of selection history are relevant, perhaps by using this monolithic framework.

We appreciate the reviewer's insightful suggestion regarding theoretical frameworks of attentional control. While Anderson (2024) proposes a monolithic theory that challenges the traditional tripartite model, our study deliberately maintains a pragmatic approach. The main purpose of our experiment is empirically investigating the mechanisms of learned distractor suppression, rather than adjudicating between competing theoretical models.

We agree that selection history is not a unitary construct but comprises multiple subcomponents, including reward associations, stimulus-response habit learning, and statistical learning. In this context, our study specifically focuses on statistical learning as a key mechanism of distractor suppression. By explicitly acknowledging the multifaceted nature of selection history and referencing Anderson's monolithic perspective, we invite readers to consider the theoretical implications while maintaining our research's primary focus on empirical investigation. To this end, we have modified the manuscript to read (see page 3):

"The present study investigates the mechanisms underlying statistical learning, specifically learned distractor suppression, which represents one critical subcomponent of selection history. While theoretical models like the tripartite framework and the recent monolithic theory (Anderson, 2024) offer complementary perspectives on attentional control, our investigation focuses on empirically characterizing the statistical learning mechanisms underlying learned distractor suppression."

(2) The authors discuss previous demonstrations of location-based and feature-based learned distractor suppression. The authors admit that there have been a large number of studies but seem to mainly cite those that were conducted by the authors themselves (with the exception being Vatterott & Vecera, 2012). For example, there are other studies investigating location-based suppression (Feldmann-Wüstefeld et al., 2021; Sauter et al., 2021), feature-based suppression (Gaspelin & Luck, 2018a; Stilwell et al., 2022; Stilwell & Gaspelin, 2021; Vatterott et al., 2018), or both (Stilwell et al., 2019). The authors do not cite Gaspelin and colleagues at all in the manuscript, despite claiming that singleton-based suppression is not proactive.

We appreciate your pointing out the need for a more comprehensive citation of the literature on learned distractor suppression, particularly with respect to location-based and feature-based suppression. In response to your comment, we have now expanded the reference list on page 4 to include relevant studies that further support our discussion of both location-based and feature-based suppression mechanisms.

(3) The authors use the terms "proactive" and "reactive" suppression without taking into consideration the recent terminology paper, which one of the current authors, Theeuwes, helped to write (Liesefeld et al., 2024, see Figure 8). The terms proactive and reactive suppression need to be defined relative to a time point. The authors need to be careful in defining proactive suppression as prior to the first shift of attention, but after the stimuli appear and reactive suppression as after the first shift of attention and after the stimuli appear. Thus, the critical time point is the first shift of attention. Does suppression occur before or after the first shift of attention? The authors could alleviate this by using the term "stimulus-triggered suppression" to refer to "suppression that occurs after the distractor appears and before it captures attention" (Liesefeld et al., 2024).

Thank you for pointing out that this was insufficiently clear in the previous version. In the revised version we specifically refer to the recent terminology paper on page 5 to make clear that suppression could theoretically occur at three distinct moments in time, and that the present paper was designed to dissociate between suppression before or after the first shift of attention.

(4) Could the authors justify why the circle stimulus (2° in diameter) was smaller than the diamonds (2.3° x 2.3°)? Are the stimuli equated for the area? Or, for width and height? Doesn't this create a size singleton target on half of all trials (whenever the target is a circle) in addition to the lone circle being a shape singleton? Along these lines, could the authors justify why the colors were used and not equiluminant? This version of red is much brighter than this version of green if assessed by a spectrophotometer. Thus, there are sensory imbalances between the colors. Further, the grey used as the ping is likely not equiluminant to both colors. Thus, the grey "ping" is likely dimmer for red items but brighter for green items. Is this a fair "ping"?

Thank you for raising these important points. We chose, as is customary in this experimental paradigm (e.g., Huang et al., 2023; Duncan et al., 2023), to make the diamond slightly larger (2.3° x 2.3°) than the circle (2° in diameter) to ensure a better visual match in overall size appearance. If the circle and diamond stimuli were equated strictly in terms of size (both at 2°), the diamond would appear visually smaller due to the differences in geometric shape. By adjusting the dimensions slightly, we aimed to minimize any unintentional differences in perceptual salience.

As for the colors used in the experiment, the reviewer is right that there might be sensory imbalances between the red and green stimuli, with red appearing brighter than green based on measurements such as spectrophotometry. To ensure that any effects couldn’t be explained by sensory imbalance in the displays, we randomized target and distractor colors across trials, meaning that roughly half the trials had a red distractor and half had a green distractor. This randomization should have mitigated any systematic biases caused by color differences.

We appreciate your feedback and have clarified these points in method section in the revised manuscript on page 22:

"Please note that although the colors were not equiluminant, the target and distractor colors were randomized across trials such that roughly half the trials had a red distractor, and half had a green distractor. This randomization process should help mitigate any systematic biases this may cause."

(5) For the eye movement artifact rejection, the authors use a relatively liberal rejection routine (i.e., allowing for eye movements up to 1.2° visual angle and a threshold of 15 μV). Given that every 3.2 μV deviation in HEOG corresponds to ~ ± 0.1° of visual angle (Lins, et al., 1993), the current oculomotor rejection allows for eye movements between 0.5° and 1.2° visual angle to remain which might allow for microsaccades (e.g., Poletti, 2023) to contaminate the EEG signal (e.g., Woodman & Luck, 2003).

The reviewer correctly points out that our eye rejection procedure, which is the same as in our previous work (e.g., Duncan et al., 2023), still allows for small, but systematic biases in eye position towards the remembered location and potentially towards or away from the high probability distractor location. While we cannot indefinitely exclude this possibility, we believe this is unlikely for the following reasons. First, although there is a link between microsaccades and covert attention, it has been demonstrated that subtle biases in eye position cannot explain the link between alpha activity and the content of spatial WM (Foster et al., 2016, 2017). Specifically, Foster et al. (2017) found no evidence for a gaze-position-related CTF, while an analysis on that same data yielded clear target related CTFs. Similarly, within the present data set there was no evidence that the observed revival induced by the ping display could be attributed to systematic changes in gaze position, as a multivariate cross-session decoding analysis with x,y positions from the tracker did not yield reliable above-chance decoding of the location in memory.

Author response image 1.

(6) The authors claim that "If the statistically learned suppression was spatial-based and feature-blind, one would also expect impaired target processing at the high-probability location." (p. 7, lines 194-195). Why is it important that suppression is feature-blind here? Further, is this a fair test of whether suppression is feature-blind? What about inter-trial priming of the previous trial? If the previous trial's singleton color repeated RTs might be faster than if it switched. In other words, the more catastrophic the interference (the target shape, target color, distractor shape, distractor color) change between trials, the more RTs might slow (compared with consistencies between trials, such that the target and distractor shapes repeat and the target and distractor colors repeat). Lastly, given the variability across both the shape and color dimensions, the claim that this type of suppression is feature-blind might be an artifact of the design promoting location-based instead of feature-based suppression.

Thank you for raising this point. In the past we have used the finding that learned suppression was not specific to distractors, but also generalized to targets to argue in favor of proactive (or stimulus triggered) suppression. However, we agree that given the current experimental parameters it may be an oversimplification to conclude that the effect was feature-blind based on the impaired target processing as observed here. As this argument is also not relevant to our main findings, we have removed this interpretation and simply report that the effect was observed for both distractor and targets. Nevertheless, we would like to point out that while inter-trial priming could influence reaction times, the features of both target and distractors (shape and color) were randomly assigned on each trial. This should mitigate consistent feature repetitions effects. Additionally, previous research has demonstrated that suppression effects persist even when immediate feature repetitions are controlled for or statistically accounted for (e.g., Wang & Theeuwes 2018 JEP:HPP; Huang et al., 2021 PB&R).

(7) The authors should temper claims such as "suppression occurs only following attentional enhancement, indicating a reactive suppression mechanism rather than proactive suppression." (p. 15, lines 353-353). Perhaps this claim may be true in the current context, but this claim is too generalized and not supported, at least yet. Further, "Within the realm of learned distractor suppression, an ongoing debate centers around the question of whether, and precisely when, visual distractors can be proactively suppressed. As noted, the idea that learned spatial distractor suppression is applied proactively is largely based on the finding that the behavioral benefit observed when distractors appear with a higher probability at a given location is accompanied by a probe detection cost (measured via dot offset detection) at the high probability distractor location (Huang et al., 2022, 2023; Huang, Vilotijević, et al., 2021)." (p. 15, lines 355-361). Again, the authors should either cite more of the opposing side of the debate (e.g., the signal suppression hypothesis, Gaspelin & Luck, 2019 or Luck et al., 2021) and the many lines of converging evidence of proactive suppression) or temper the claims.

Thank you for your constructive feedback regarding our statements on suppression mechanisms. We acknowledge that our original claim was intended to reflect our specific findings within the context of this study and was not meant to generalize across all research in the field. To prevent any misunderstanding, we have tempered our claims to avoid overgeneralization by clarifying that our findings suggest a tendency toward reactive suppression within the specific experimental conditions we investigated (see page 17).

Furthermore, learned distractor suppression is multifaceted, encompassing both feature-based suppression (as proposed by the signal suppression hypothesis) and spatial-based suppression (as examined in the current study). The signal suppression hypothesis provides proactive evidence related to the suppression of specific feature values (Gaspelin et al., 2019; Gaspelin & Luck, 2018b; Stilwell et al., 2019). We have incorporated references to these studies to offer a more comprehensive perspective on the ongoing debate at a broader level (see page 17).

(8) "These studies however, mainly failed to find evidence in support of active preparatory inhibition (van Moorselaar et al., 2020, 2021; van Moorselaar & Slagter, 2019), with only one study observing increased preparatory alpha contralateral to the high probability distractor location (Wang et al., 2019)." (p. 15, lines 367-370). This is an odd phrasing to say "many studies" have shown one pattern (citing 3 studies) and "only" one showing the opposite, especially given these were all from the current authors' labs.

Agreed. We have rewritten this text on page 17.

“These studies however, failed to find evidence in support of active preparatory inhibition as indexed via increased alpha power contralateral to the high probability distractor location  (van Moorselaar et al., 2020, 2021; van Moorselaar & Slagter, 2019; but see Wang et al., 2019).”

(9) Could the authors comment on why total power was significantly above baseline immediately (without clearer timing marks, ~10-50 ms) after the onset of the cue (Figure 3)? Is this an artifact of smearing? Further, it appears that there is significant activity (as strong as the evoked power of interest) in the baseline period of the evoked power when the memory item is presented on the vertical midline in the upper visual field (this is also true, albeit weaker, for the memory cue item presented on the horizontal midline to the right). This concern again appears in Figure 4 where the Alpha CTF slope was significantly below or above the baseline prior to the onset of the memory cue. Evoked Alpha was already significantly higher than baseline in the baseline period. In Figure 5, evoked power is already higher and different for the hpl than the lpls even at the memory cue (and before the memory cue onsets). There are often periods of differential overlap during the baseline period, or significant activity in the baseline period or at the onset of the critical, time-locked stimulus array. The authors should explain why this might be (e.g., smearing).

Thank you for pointing this out. As suggested by the reviewer, this ‘unexpected’ pre-stimulus decoding is indeed the result of temporal smearing induced by our 5th order Butterworth filter. The immediate onset of reliable tuning (sometimes even before stimulus onset) is then also a typical aspect of studies that track tuning profiles across time in the lower frequency bands such as alpha (van Moorselaar & Slagter 2019; van Moorselaar et al., 2020; Foster et al., 2016).

Indeed, visual inspection also suggests that evoked activity tracked items at the top of the screen, an effect that is unlikely to result from temporal smearing as it is temporally interrupted around display onset. However, it is important to note that CTFs by location are based on far fewer trials, making them inherently noisier. The by-location plots primarily serve to show that the observed pattern is generally consistent across locations. In any case, given that the high probability distractor location was counterbalanced across participants it did not systematically influence our results.

(10) Given that EEG was measured, perhaps the authors could show data to connect with the extant literature. For example, by showing the ERP N2pc and PD components. A strong prediction here is that there should be an N2pc component followed by a PD component if there is the first selection of the singleton before it is suppressed.

Thank you for your great suggestion regarding the analysis of ERP components such as N2pc and Pd. To reliably assess lateralized ERP components like N2pc or Pd the high probability location must be restricted to static lateralized positions (e.g., on the horizontal midline such as Wang et al., 2019). In contrast, our study was designed to utilize an inverted encoding model to investigate the mechanisms underlying spatial suppression. To avoid bias in training the spatial model toward specific spatial locations (see also the previous comment), we counterbalanced the high-probability location across participants, ensuring an equal distribution of high-probability locations within the sample. Given this counterbalanced design, it was not feasible to reliably assess these components within the scope of the current study. Yet, we agreed with the reviewer that it would be of theoretical interest to examine Pd and N2pc evoked by the search display, particularly in this scenario where suppression has been triggered prior to search onset.

(11) Figure 2 (behavioral results) is difficult to see (especially the light grey and white bars). A simple fix might be to outline all the bars in black.

Thank you! We have incorporated your suggestion by outlining all the bars on page 10.

Reviewer #3 (Recommendations For The Authors):<br /> (1) I'm wondering about the link between the memory task and the search task.  I think the interpretation of the data should include more discussion of the fact that much of the search literature doesn't involve simultaneously holding an unrelated location in memory.  How might that change the results?

For example - what happens behaviorally on the subset of trials in which the location to be held in memory is near the high probability distractor location?  All the behavioral data is more or less compartmentalized, but I think some behavioral analysis of this and related questions might be quite useful.  I know there are comparisons of behavior in single vs. dual-task cases (for the memory task at least), but I think the analyses could go deeper.

Thank you for your great suggestion. To investigate the potential interactions between the spatial memory task and the visual search task, we conducted additional analyses on the behavioral data. First, we examined whether memory recall was influenced by the spatial distance (dist0 to dist4) between the memory cue location and the high-probability distractor location. As shown in the figure below, memory recall is not systematically biased either toward or away from the high-probability distractor location (p = .562, ηp² = .011).

We also assessed how the memory task might affect search performance. Specifically, we plotted reaction times as a function of the spatial overlap between the memory cue location and any of the search items, separating trials by distractor-present (match-target, match-distractor, match-neutral) and distractor-absent (match-target, match-neutral) conditions. Although visually the result pattern seems to suggest that search performance was facilitated when the memory cue spatially overlapped with the target and interfered with when it overlapped with the distractor, this pattern did not reach statistical significance (distractor-present: p = .249, ηp² = .002; distractor-absent: p = .335, ηp² = .002). We have now included these analyses in our supplemental material.

Beyond additional data analyses, there are also theoretical questions to be asked.  For example, one could argue that in order to maintain a location near or at the high probability distractor location in working memory, the priority map would have to shift substantially. This doesn't necessarily mean that proactive suppression always occurs in search when there is a high probability location. Instead, one could argue that when you need to maintain a high probability location in memory but also know that this location might contain a distractor, the representation necessarily looks quite different than if there were no memory tasks.  Maybe there are reasons against this kind of interpretation but more discussion could be devoted to it in the manuscript. I guess another way to think of this question is - how much is the ping showing us about attentional priority for search vs. attentional priority for memory, or is it simply a combination of those things, and if so, how might that change if we could ping the attentional priority map without a simultaneous memory task?

Thank you for this valuable suggestion. The aim of our study was to explore how the CTFs elicited by the memory cue were influenced by the search task. We employed a simultaneous memory task because directly measuring CTFs in relation to the search task was not feasible, as the HPL typically does not vary within individual participants. Consequently, CTFs locked to placeholder onsets could reflect arbitrary differences between (subgroups of) participants rather than true differences in the HPL. To address this, we combined the search task with a VWM task, leveraging the fact that location-specific CTFs can reliably be elicited by a memory cue and that the location of this cue relative to the HPL can be systematically varied within participants (Foster et al., 2016, 2017; van Moorselaar et al., 2018). This approach allowed us to examine the CTFs elicited by the memory cue and how these were modulated by their distance from the HPL.

While it is theoretically possible that the observed changes resulted from alterations in how the memory cue was maintained in memory only, this explanation seems unlikely, for memory performance (recall) did not vary as a function of the cue's distance from the HPL, suggesting that the distance-related changes in the CTFs are reflections of both tasks. Moreover, distractor learning typically occurs without awareness (Gao & Theeuwes 2022; Wang & Theeuwes 2018). It is difficult to understand how such unconscious processes could lead to anticipations in the memory task and subsequently modulate the representation of the consciously remembered memory cue only. We therefore believe that if we would have pinged the attentional priority map without a simultaneous memory task, the results would have been similar to those obtained in the present experiment, indicating stronger tuning at the HPL. Yet, this work still needs to be done.

To address this comment, we have added a paragraph on p. 18:

“However, two alternative explanations warrant consideration. First, one could argue that observed modulations in the revived CTFs do not provide insight into the mechanisms underlying distractor suppression but instead reflect changes in the memory representation itself, potentially triggered by the anticipation of the HPL in the search task. According to this view, the changes in the revived CTFs would be unrelated to how search performance (in particular distractor suppression) was achieved. While this is theoretically possible, we believe it to be unlikely. Memory performance (recall) did not vary as a function of the cue's distance from the HPL, whereas the revived CTFs did, indicating that these changes likely reflect contributions from both tasks. Additionally, distractor learning typically occurs without conscious awareness (Gao & Theeuwes 2022; Wang & Theeuwes 2018). It is difficult to conceive how such unconscious processes could produce anticipatory effects in the memory task and selectively modulate the representation of the consciously remembered memory cue. Second, the apparent lack of suppression and the presence of a pronounced tuning at the high-probability distractor location could actually reflect a proactive mechanism that manifests in a way that seems reactive due to the dual-task nature of our experiment.”

(2) When the distractor appears at a particular location with a high probability it necessarily means that intertrial effects differ between high and low probability distractor locations.  Consecutive trials with a distractor at the same location are far more frequent in the high probability condition.  You may not have enough power to look at this, and I know this group has analyzed this behaviorally in the past, but I do wonder how much that influences the EEG data reported here.  Are CTFs also sensitive to distractors/targets from the most recent trial?  And does that contribute to the overall patterns observed here?

Thank you for your thoughtful comment. Indeed, Statistical distractor learning studies naturally involve a higher proportion of intertrial effects for high-probability distractors compared to low-probability ones. Previous research, including the present study, has demonstrated that while distractor location improves performance—shown by faster response times (t(23) = 6.32, p < .001, d = 0.33) and increased accuracy (t(23) = 4.21, p < .001, d = 0.86)—intertrial effects alone cannot fully account for the learned suppression effects induced by spatial distractor imbalances. This analysis in now reflected in the revised manuscript on page 9.

However, as noted by the reviewer, this leaves uncertain to what extent the neural indices of statistical learning, in this case the modulation of channel tuning functions, capture the effects of interest beyond the contributions of intertrial priming. To address this issue, one possible approach is to rerun the CTF analysis after excluding trials with location repetitions. Since the distractor location is unknown to participants at the time the CTF is revived by the placeholder, we removed trials where the memory cue location repeated the distractor location from the preceding trial, rather than trials with distractor location repetitions between consecutive trials. Our analyses indicate that after trials removal (~ 9% of overall trials), the spatial gradient pattern in the CTF slopes remains similar. However, the cluster-based permutation analysis fails to reveal any significant findings, and a one-sample t-test on the slopes averaged within the 100 ms time window of interest yields a p-value of 0.106. While this could suggest that the current pattern is influenced by distractor-cue repetition, it is more likely that the trial removal resulted in an underpowered analysis. To investigate this, we randomly removed an equivalent number of trials (9%), which similarly resulted in insignificant findings, although the overall result pattern remained comparable (p = 0.066 for the one-sample t-test on the slopes average within the interested time window of 100 ms).

Author response image 2.

Also, in our previous pinging study we observed that, despite the trial imbalance, decoding was approximately equal between high probability trailing (i.e., location intertrial priming) and non-trailing trials, suggesting that the ping is able to retrieve the priority landscape that build up across longer timescales.

(3) Maybe there is too much noise in the data for this, but one could look at individual differences in the magnitude of the high probability distractor suppression and the magnitude of the alpha CTF slope.  If there were a correlation here it would bolster the argument about the relationship between priority to the distractor location and subsequent behavior reduction of interference from that distractor.  

Thank you for this valuable suggestion. We investigated whether there was a correlation between the average gradient slope during the time window in which the placeholder revived the memory representation and the average distance slope in reaction times for the learned suppression effect. This correlation was not significant (r = .236, p = 0.267), which is perhaps expected given the potential noise levels, as noted by the reviewer. Furthermore, while the learned suppression effect is robust at the group level, its predictive value for individual-level performance has been shown to be limited (Ivanov et al., 2024; Hedge et al., 2018). Consequently, we chose not to include this analysis in the manuscript (see also our response to comment 2 by reviewer 2).

(4) The results sections are a bit dense in places, especially starting at the bottom of page 11.  For readers who are familiar with the general questions being asked but less so with the particular time-frequency analyses and CTF approaches being used (like myself), I think a bit more time could be spent setting up these analyses within the results section to make extra clear what's going on.

Thank you for your feedback regarding the clarity of our Results section. We have revised this section to make it more understandable and easier to follow, especially for readers who may be less familiar with the specific time-frequency analyses and modeling approaches used in our study. Specifically, we have provided additional interpretations alongside the reported results from page 10 to page 13 to aid comprehension and ensure that the methodology and findings are accessible to a broader audience. Additionally, we have revised the figure notes to further enhance clarity and understanding.

Other comments:

Abstract: "a neutral placeholder display was presented to probe how hidden priority map is reconfigured..."  i think the word "the" is missing before "priority map"

Thank you. We have added the word “the” before “hidden priority map”.

p. 4, Müller's group also has a number of papers that demonstrate how learned distractor regularities impact search (From the ~2008-2012 range, probably others as well), it might be worth citing a few here.

Thank you for your suggestion. In the revised manuscript, we have added citations to several key papers from Muller’s group on page 4 as well as other research groups.

p.5 - Chang et al. (2023) seems highly relevant to the current study (and consistent with its results) - depending on word limits, it might make sense to expand the description of this in the introduction to make clear how the present study builds upon it

Thank you! We have expanded the discussion of Chang et al. (2023) on page 5 to provide more detailed elaboration of their study and its relevance to our work.

p. 7 - maybe not for the current study, but I do wonder whether the distortion of spatial memory by the presence of the search task occurs only when there is a relevant regularity in the search task. In other words, if the additional singleton task had completely unpredictable target and distractor locations, would there be memory distortions?  Possibly for the current dataset, the authors could explore whether the behavioral distortion is systematically towards or away from the high probability distractor location.

Thank you for your insightful suggestion. Following your recommendation, we conducted an additional analysis to examine memory recall as a function of the distance between the memory cue location and the high-probability distractor location. Figure S1A illustrates the results, depicting memory recall deviation across various distances (dist0 to dist4) from the high-probability distractor location.

Our statistical analysis indicates that memory recall is not systematically biased either towards or away from the high-probability distractor location (p = .562, η_p² = .011). This finding suggests that spatial memory recall remains relatively stable and is not heavily influenced by the presence of regularities in the distractor locations.

p. 7 - in addition to stats it would be helpful to report descriptive statistics for the high probability vs. other distractor location comparisons

Thank you! We have added descriptive statistics on page 8 and page 9.

p. 19, "64%" repeated unnecessarily - also, shouldn't it be 65% if it's 5% at each of the other seven locations?

Thank you. This is now corrected in the revised manuscript.

p. 20 "This process continued until participants demonstrated a thorough understanding of the assigned tasks" Were there objective criteria to measure this?

Thank you for pointing out this issue. To clarify, objective criteria were indeed used to assess participants’ readiness to proceed. Specifically:

For the training phase practice trials, participants were required to achieve an average memory recall deviation of less than 13°.

For the test phase practice trials, participants needed to demonstrate a minimum of 65% accuracy in the search task. In addition, participants were asked to verbally confirm their understanding of the task goals with the experimenter before proceeding.

We have revised the manuscript to clearly indicate these criteria on p. 23.

p. 21 "P-values were Greenhouse-Geiser corrected in case where the..." I think "case" should be "cases"

Thank you. We have corrected this in the revised manuscript.

Author response:

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

Public Reviews: 

Reviewer #1 (Public review): 

Koren et al. derive and analyse a spiking network model optimised to represent external signals using the minimum number of spikes. Unlike most prior work using a similar setup, the network includes separate populations of excitatory and inhibitory neurons. The authors show that the optimised connectivity has a like-to-like structure, which leads to the experimentally observed phenomenon of feature competition. The authors also examine how various (hyper)parameters-such as adaptation timescale, the excitatory-to-inhibitory cell ratio, regularization strength, and background current-affect the model. These findings add biological realism to a specific implementation of efficient coding. They show that efficient coding explains, or at least is consistent with, multiple experimentally observed properties of excitatory and inhibitory neurons. 

As discussed in the first round of reviews, the model's ability to replicate biological observations such as the 4:1 ratio of excitatory vs. inhibitory neurons hinges on somewhat arbitrary hyperparameter choices. Although this may limit the model's explanatory power, the authors have made significant efforts to explore how these parameters influence their model. It is an empirical question whether the uncovered relationships between, e.g., metabolic cost and the fraction of excitatory neurons are biologically relevant.

The revised manuscript is also more transparent about the model's limitations, such as the lack of excitatory-excitatory connectivity. Further improvements could come from explicitly acknowledging additional discrepancies with biological data, such as the widely reported weak stimulus tuning of inhibitory neurons in the primary sensory cortex of untrained animals.

We thank the Reviewer for their insightful characterization of our paper and for further suggestions on how to improve it. We have now further improved the transparency about model’s limitations and we explicitly acknowledged the discrepancy with biological data about connection probability and about the selectivity of inhibitory neurons (pages 4 and 15).

Reviewer #2 (Public review): 

Summary: 

In this work, the authors present a biologically plausible, efficient E-I spiking network model and study various aspects of the model and its relation to experimental observations. This includes a derivation of the network into two (E-I) populations, the study of single-neuron perturbations and lateral-inhibition, the study of the effects of adaptation and metabolic cost, and considerations of optimal parameters. From this, they conclude that their work puts forth a plausible implementation of efficient coding that matches several experimental findings, including feature-specific inhibition, tight instantaneous balance, a 4 to 1 ratio of excitatory to inhibitory neurons, and a 3 to 1 ratio of I-I to E-I connectivity strength.

Strengths: 

While many network implementations of efficient coding have been developed, such normative models are often abstract and lacking sufficient detail to compare directly to experiments. The intention of this work to produce a more plausible and efficient spiking model and compare it with experimental data is important and necessary in order to test these models. In rigorously deriving the model with real physical units, this work maps efficient spiking networks onto other more classical biophysical spiking neuron models. It also attempts to compare the model to recent single-neuron perturbation experiments, as well as some long-standing puzzles about neural circuits, such as the presence of separate excitatory and inhibitory neurons, the ratio of excitatory to inhibitory neurons, and E/I balance. One of the primary goals of this paper, to determine if these are merely biological constraints or come from some normative efficient coding objective, is also important. Lastly, though several of the observations have been reported and studied before, this work arguably studies them in more depth, which could be useful for comparing more directly to experiments.

Weaknesses: 

This work is the latest among a line of research papers studying the properties of efficient spiking networks. Many of the characteristics and findings here have been discussed before, thereby limiting the new insights that this work can provide. Thus, the conclusions of this work should be considered and understood in the context of those previous works, as the authors state. Furthermore, the number of assumptions and free parameters in the model, though necessary to bring the model closer to biophysical reality, make it more difficult to understand and to draw clear conclusions from. As the authors state, many of the optimality claims depend on these free parameters, such as the dimensionality of the input signal (M=3), the relative weighting of encoding error and metabolic cost, and several others. This raises the possibility that it is not the case that the set of biophysical properties measured in the brain are accounted for by efficient coding, but rather that theories of efficient coding are flexible enough to be consistent with this regime. With this in mind, some of the conclusions made in the text may be overstated and should be considered in this light.

Conclusions, Impact, and additional context: 

Notions of optimality are important for normative theories, but they are often studied in simple models with as few free parameters as possible. Biophysically detailed and mechanistic models, on the other hand, will often have many free parameters by their very nature, thereby muddying the connection to optimality. This tradeoff is an important concern in neuroscientific models. Previous efficient spiking models have often been criticized for their lack of biophysically-plausible characteristics, such as large synaptic weights, dense connectivity, and instantaneous communication. This work is an important contribution in showing that such networks can be modified to be much closer to biophysical reality without losing their essential properties. Though the model presented does suffer from complexity issues which raise questions about its connections to "optimal" efficient coding, the extensive study of various parameter dependencies offers a good characterization of the model and puts its conclusions in context.

We thank the Reviewer for their thorough and accurate assessment of our paper.  

Reviewer #3 (Public review): 

Summary: 

In their paper the authors tackle three things at once in a theoretical model: how can spiking neural networks perform efficient coding, how can such networks limit the energy use at the same time, and how can this be done in a more biologically realistic way than previous work. 

They start by working from a long-running theory on how networks operating in a precisely balanced state can perform efficient coding. First, they assume split networks of excitatory (E) and inhibitory (I) neurons. The E neurons have the task to represent some lower dimensional input signal, and the I neurons have the task to represent the signal represented by the E neurons. Additionally, the E and I populations should minimize an energy cost represented by the sum of all spikes. All this results in two loss functions for the E and I populations, and the networks are then derived by assuming E and I neurons should only spike if this improves their respective loss. This results in networks of spiking neurons that live in a balanced state, and can accurately represent the network inputs. 

They then investigate in depth different aspects of the resulting networks, such as responses to perturbations, the effect of following Dale's law, spiking statistics, the excitation (E)/inhibition (I) balance, optimal E/I cell ratios, and others. Overall, they expand on previous work by taking a more biological angle on the theory and show the networks can operate in a biologically realistic regime.

Strengths: 

* The authors take a much more biological angle on the efficient spiking networks theory than previous work, which is an essential contribution to the field

* They make a very extensive investigation of many aspects of the network in this context, and do so thoroughly

* They put sensible constraints on their networks, while still maintaining the good properties these networks should have

Weaknesses: 

* One of the core goals of the paper is to make a more biophysically realistic network than previous work using similar optimization principles. One of the important things they consider is a split into E and I neurons. While this works fine, and they consider the coding consequences of this, it is not clear from an optimization perspective why the split into E and I neurons and following Dale's law would be beneficial. This would be out of scope for the current paper however.

* The theoretical advances in the paper are not all novel by themselves, as most of them (in particular the split into E and I neurons and the use of biophysical constants) had been achieved in previous models. However, the authors discuss these links thoroughly and do more in-depth follow-up experiments with the resulting model. 

Assessment and context: 

Overall, although much of the underlying theory is not necessarily new, the work provides an important addition to the field. The authors succeeded well in their goal of making the networks more biologically realistic, and incorporate aspects of energy efficiency. For computational neuroscientists this paper is a good example of how to build models that link well to experimental knowledge and constraints, while still being computationally and mathematically tractable. For experimental readers the model provides a clearer link of efficient coding spiking networks to known experimental constraints and provides a few predictions.

We thank the Reviewer for a positive assessment and for pointing out the merits of our work.

Recommendations for the authors:  

Reviewer #1 (Recommendations for the authors):

The authors have addressed my previous concerns, and I agree that the manuscript has improved. However, I believe they could still do more to acknowledge two notable mismatches between the model and experimental data.

(1) Stimulus selectivity of excitatory and inhibitory neurons 

In the model, excitatory and inhibitory neurons exhibit similar stimulus selectivity, which appears inconsistent with most experimental findings. The authors argue that whether inhibitory neurons are less selective remains an open question, citing three studies in support. However, only one of these studies (Ranyan) was conducted in primary sensory cortex and it is, to my knowledge, one of the few papers showing this (indeed, it's often cited as an exception). The other two studies (Kuan and Najafi) recorded from the parietal cortex of mice trained on decision making tasks, and therefore seem less relevant to the model.

In contrast to the cited studies, the overwhelming majority of the work has found that inhibitory neurons in sensory cortex, in particular those expressing Parvalbumin, are less stimulus selective than excitatory cells. And this is indeed the prevailing view, as summarized by the review from Hu et al. (Science, 2014): "PV+ interneurons exhibit broader orientation tuning and weaker contrast specificity than pyramidal neurons." This view emerged from numerous classical studies, including Sohya et al. (J. Neurosci., 2007), Cardin (J. Neurosci., 2007), Nowak (Cereb. Cortex, 2008), Niell et al. ( J. Neurosci., 2008), Liu (J. Neurosci., 2009), Kerlin (Neuron, 2010), Ma et al. (J. Neurosci., 2010), Hofer et al. (Nature Neurosci. 2011), and Atallah et al. (Neuron 2012). Weak inhibitory tuning has been confirmed by recent studies, such as Sanghavi & Kar (biorxiv 2023), Znamenskiy et al. (Neuron 2024), and Hong et al. (Nature, 2024).

The authors should acknowledge this consensus and cite the conflicting evidence. Failing to do so is cherry picking from the literature. Since training can increase the stimulus selectivity of PV+ neurons to that of Pyr levels, also in primary visual cortex (Khan et al. Neuron 2018), a favourable interpretation of the model is that it represents a highly optimized, if not overtrained, state.

We have carefully considered the literature cited by the Reviewer. We agree with the interpretation that stimulus selectivity of inhibitory neurons in our model is higher than the stimulus selectivity of Parvalbumin-positive inhibitory neurons in the primary sensory cortex of naïve animals. We have edited the text in Discussion (page 14).

(2) Connection probability 

The manuscript claims that "rectification sets the overall connection probability to 0.5, consistent with experimental results (Pala & Petersen; Campagnola et al.)." However, the cited studies, and others, report significantly lower probabilities, except for Pyr-PV (E-I connections in the model). For example, Campagnola et al. measured PV-Pyr connectivity at 34% in L2/3 and 20% in L5.

It's perfectly acceptable that the model cannot replicate every detail of biological circuits. But it's important to be cautious when claiming consistency with experimental data.

Here as well, we agree with the Reviewer that the connection probability of 0.5 is consistent with reported connectivity of Pyr-PV neurons, but less so with reported connectivity of PV-Pyr neurons. We have now qualified our claim about compatibility of the connection probability in our model with empirical observations more precise (page 4).

Reviewer #2 (Recommendations for the authors): 

I commend the authors for an extremely thorough and detailed rebuttal, and for all of the additional work put in to address the reviewer concerns. For the most part, I am satisfied with the current state of the manuscript. 

We thank the Reviewer for recognizing our effort to address the first round of Reviews to our best ability.

Here are some small points still remaining that I think the authors should address: 

(1) Pg. 8, "We verified the robustness of the model to small deviations from the optimal synaptic weights" - while the authors now cite Calaim et al. 2022 in the discussion, its relevance to several of the results justify its inclusion in other places. Here is one place where the authors test something that was also studied in this previous paper.

The Reviewer is correct that Calaim et al. (eLife 2022) addressed the robustness of synaptic weights, and we now cited this study when describing our results on jiVering of synaptic connections (page 8).

(2) Pg. 9, "In our optimal E-I network we indeed found that optimal coding efficiency is achieved in absence of within-neuron feedback or with weak adaptation in both cell types" Pg. 10, "the absence of within-neuron feedback or the presence of weak and short-lasting spike-triggered adaptation in both E and I neurons are optimally efficient solutions" The authors seem to state that both weak adaptation and no adaptation at all are optimal. In contrast to the rest of the results presented, this is very vague and does not give a particular level of adaptation as being optimal. The authors should make this more clear. 

We agree that the text about optimal level of adaptation was unclear. The optimal solution is no adaptation, while weak and short-lasting adaptation define a slightly suboptimal, yet still efficient, network state, as now stated on page 10.

(3) Pg. 13, "In summary our analysis suggests that optimal coding efficiency is achieved with four times more E neurons than I neurons and with mean I-I synaptic efficacy about 3 times stronger..." --- claims such as these are still too strong, in my opinion. It is rather the case that the particular ratio of E to I neurons and connections strengths can be made consistent with an optimally efficient regime.

We agree here as well. We have revised the text (page 13) to beVer explain our results.

(4) Pg. 14, "firing rates in the 1CT model were highly sensitive to variations in the metabolic constant" (Fig. 8I, as compared to Fig. 6C). This difference between the 1CT and E-I networks is striking, and I would suspect it is due to some idiosyncrasies in the difference between the two models (e.g., the relative amount of delay that it takes for lateral inhibition to take effect, or the fact that E-E connections have not been removed in this model). The authors should ideally back up this result with some justified explanation. 

We agree with Reviewer that the delay for lateral inhibition in the E-I model is twice that of the 1CT model and that the E-I model gains stability from the lack of E-E connectivity. Furthermore, the tuning is stronger in I compared to E neurons in the E-I model, which contributes to making the E-I network inhibition-dominated (Fig. 1H). In contrast, the average excitation and inhibition in the 1CT model are of exactly the same magnitude. The property of being inhibition-dominated makes the E-I model more stable. We report these observations in the revised text (pages 14-15). 

Reviewer #3 (Recommendations for the authors): 

Overall my points were very well responded to and I removed most of my weaknesses.

I appreciate the authors implementing my suggested analysis change for Figure 8, and I find the result very clear. I would further suggest they add a bit of text for the reader as to why this is done. For a new reader without much knowledge of these networks at first it seems the inhibitory population is very good at representation in fig 8G: so why is it not further considered in fig 8H?

We thank the reviewer for providing further suggestions. We now clarified in the text why only the excitatory population of the E-I model is considered in E-I vs 1 cell type model comparison (page 14). 

Thanks for sharing the code. From a quick browse through it looks very manageable to implement for follow up work, although some more guidance for how to navigate the quite complicated codebase and how to reproduce specific paper results would be helpful.

We have also updated the code repository, where we have included more complete instructions on how to reproduce results of each figure. We renamed the folders with the computer code so that they point to a specific figure in the paper. The repository has been completed with the output of the numerical simulations we run, which allows immediate replot of all figures. We have deposited the repository at Zenodo to have the final version of the code associated with the DOI ttps://doi.org/10.5281/zenodo.14628524. This is mentioned in the section Code availability (page 17).

Author response:

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

Reviewer 1 Public Review:

Summary

This very short paper shows a greater likelihood of C->U substitutions at sites predicted to be unpaired in the SARS-CoV-2 RNA genome, using previously published observational data on mutation frequencies in  SARS-CoV-2 (Bloom and Neher, 2023).

General comments

A preference for unpaired bases as a target for APOBEC-induced mutations has been demonstrated previously in functional studies so the finding is not entirely surprising. This of course assumes that A3A or other APOBEC is actually the cause of the majority of C->U changes observed in SARS-CoV-2 sequences.

I'm not sure why the authors did not use the published mutation frequency data to investigate other potential influences on editing frequencies, such as 5' and 3' base contexts. The analysis did not contribute any insights into the potential mechanisms underlying the greater frequency of C->U (or G->U) substitutions in the SARS-CoV-2 genome.

I have added additional discussions of mechanisms focusing on the question of whether basepairing bias is  primarily driven by secondary structure dependence of underlying mutation rates or by conservation of  secondary structure (Discussion lines 178–192) and I added a brief analysis of the 5′ and 3′ contexts of the  relationship between being basepaired in a secondary structure model and apparent mutational fitness  (Figures S1 and S2, Results lines 85–97). I found that the 5′ context of unpaired, but not paired basepairs  influences apparent mutational fitness (preference for 5′ U), and that the  is also . Additionally, there is a 3′  preference for G, indicating some CpG suppression. This contrasts to some degree with another analysis  based on counting lineage frequencies that may have lacked power to detect relatively small effects  (Simmonds  mBio  2024).

Reviewer 1 Author recommendations:

There are at least 5 publications describing the mapping/prediction of SARS-CoV-2 RNA secondary structure from 2022-2023 and their predictions are not entirely consistent. Why did the authors only refer to the Lan et al. paper?

I have added comparisons when the Lan et al secondary structure model is replaced by one of two others  derived from SHAPE data (Results lines 110–122). Unsurprisingly, similar secondary structure models give  similar results and performance is modestly higher for the models from Lan et al. This is consistent  with  their observations that DMS reactivities performed better as classifiers of SL5 and ORF1 secondary  structure (the reason I compared to this secondary structure model and reactivity data set rather than  others), but I did not go into detail on this in the revision since there are many differences in methods  beyond class of reactivity probe. For example, somewhat stronger correlation for the Vero than the Huh7  dataset in Lan  et al  could arise from combining data  from two replicates, from cell type, or from differences  in data analysis methods. It’s also a small difference and cannot be confidently distinguished from noise.

I conducted a preliminary comparison of the performance of DMS and SHAPE data for predicting mutations  where DMS data is available, but I opted against including this analysis in the manuscript for the same  reasons. Instead, I included in results and discussion comments on how, in general, reactivity data contains  information that is predictive of substitution rates that is not captured by binary secondary structure models.  I also discuss how multiple data sources can potentially be integrated to more accurately predict the impact  of a substitution on fitness (Discussion lines 195–201).

Specific substitutions are referred to as C->T and C29085T for example, but as the genome of SARS-CoV-2 is RNA, and T should be a U.

I agree and I have changed all “T” to “U” in the paper and analysis scripts. The choice of “T” was motivated  by what seemed to appear most frequently in papers on SARS-CoV-2 mutational spectra, but “U” is nearly  universal in papers on secondary structure and mutation mechanisms, so I agree it makes more sense in  this paper.

The C29085T substitution is somewhat non-canonical as it is a single base bulge in a longer duplex section of dsRNA, very unlike the favoured sites for mutation in the Nakata et al paper.

I have added a discussion of Nakata  et al ( NAR 2023) ( Introduction lines 29–32). I did not go into this depth  in the revision, but the analysis of ~2M patient sequences in Nakata  et al  also noted a high rate of UUC→UUU substitution, so the UUUC context of C29095 (shared by 3 of the 10 positions highlighted in  Nakata  et al  that had high mutation frequencies with  exogenous APOBEC3A expression) could be  interesting to investigate further.

High C29095U substitution frequency is indeed somewhat at odds with the results in that work, which found  that UC→UU substitutions to be elevated in longer single-stranded regions than the context of C29095U in  SARS-CoV-2 secondary structure models (a single unpaired base opposing three unpaired bases in an  asymmetric internal loop).

I'm not sure why DMS reactivity is considered a separate variable from pairing likelihood as one informs the other.

The intent here, which was not clear, was to show that a binary basepairing model that uses DMS  reactivities as constraints does not capture all of the information available. I have clarified this in as  described above discussing information in different reactivy datasets.

The C29095U substitution is also relavent to the consideration of DMS reactivity in addition to the resulting  secondary structure model. These are not considered as separate predictors and the reason for showing  both is mentioned in the paper: “DMS reactivity was more strongly correlated with estimated mutational  fitness than basepairing when analysis was limited to positions with detectable DMS reactivity.” I have  clarified this in the revised manuscript and also it is relevant to the discussion of a potential model  integrating all available datasets.

Reviewer 2 Public Review:

Hensel investigated the implications of SARS-CoV-2 RNA secondary structure in synonymous and nonsynonymous mutation frequency. The analysis integrated estimates of mutational fitness generated by Bloom and Neher (from publicly available patient sequences) and a population-averaged model of RNA basepairing from Lan et al (from DMS mutational profiling with sequencing, DMS-MaPseq).

The results show that base-pairing limits the frequency of some synonymous substitutions (including the most common CT), but not all: GA and AG substitutions seem unaffected by base-pairing.

The author then addressed nonsynonymous CT substitutions at base-paired positions. While there is still a generally higher estimated mutational fitness at unpaired positions, they propose a coarse adjustment to disentangle base-pairing from inherent mutational fitness at a given position. This adjustment reveals that nonsynonymous substitutions at base-paired positions, which define major variants, have higher mutational fitness.

Overall, this manuscript highlights the importance of considering RNA secondary structure in viral evolution studies.

The conclusions of this work are generally well supported by the data presented. Particularly, the author acknowledges most limitations of the analyses, and addresses them. Even though no new sequencing results were generated, the author used available data generated from the analysis of roughly seven million sequenced patient samples. Finally, the author discusses ways to improve the current available models.

There are a number of limitations of this work that should be highlighted, specifically in regard to the secondary structure data used in this paper. The Lan et al. dataset was generated using a multiplicity of infection (MOI) of 0.05, 24 hours post-infection (h.p.i.). At such a low MOI and late timepoint, viral replication is not synchronous and sequencing artifacts might be generated by cell debris and viral RNA degradation, therefore impacting the population-averaged results. In addition, the nonsynonymous base-paired positions in Figure 2 have relatively high population-averaged DMS reactivity, which suggests those positions are dynamic. Therefore, the proposed adjustment could result in an incorrect estimation of their inherent mutational fitness.

I would go further than this to say that the proposed adjustmentment  will usually  result in an incorrect  estimate. My intent is to propose an improved, but still likely incorrect, estimate by utilizing  in  vitro  data to  refine baseline mutation rates in order to obtain improved, but only coarsely adjusted, estimates of  mutational fitness. I added a note in the discussion that  in vitro  reactivities (and, consequently, secondary  structure models) may not reflect secondary structures  in vivo ( Discussion lines 204–205). I did not go  into  detail regarding the specific technical considerations mentioned here because they are outside the scope of  my expertise.

I am not sure that top-ranked non-synonymous C→U positions have particularly high DMS values after  coarse adjustment for basepairing (labeled amino acid mutations in Figure 2). Of the six common mutations  used as examples, three have minimum values in the dataset considered (which is processed  normalized/filtered data rather than raw data) and three do not have very high DMS reactivity.

However, there is clearly information in base reactivity that is not captured by a binary basepairing model,  which is indicated by residual positive correlation between DMS reactivity and mutational fitness after  adjustment. I now include a figure demonstrating this for synonymous C→U substitutions as Figure S3, and  I have tried to clarify the language throughout the manuscript to make it clear that a more accurate  adjustment is possible.

Additionally, like all such RNA probing experiments within cells, it remains difficult to deconvolve DMS/SHAPE low reactivity with RNA accessibility (e.g. from protein binding).

I agree, and in revising this manuscript it was interesting to see that Nakata  et al ( discussed above)  identified relatively large single-stranded regions with enhanced UC→UU substitution frequencies with  exogenous APOBEC3A expression, while C29095U, for example, is a single unpaired base with high DMS  reactivity and high empirical C→U substitution frequency (discussed briefly in the introduction of the revised  manuscript). Future analyses could consider heterogeneity in secondary structure as well as secondary  structures with low heterogeneity where strained conformations could have higher reactivity.

This work presents clear methods and an easy-to-access bioinformatic pipeline, which can be applied to other RNA viruses. Of note, it can be readily implemented in existing datasets. Finally, this study raises novel mechanistic questions on how mutational fitness is not correlated to secondary structure in the same way for every substitution.

Overall, this work highlights the importance of studying mutational fitness beyond an immune evasion perspective. On the other hand, it also adds to the viral intrinsic constraints to immune evasion.

Reviewer 2 Author recommendations:

Even though the experiment was not performed in this manuscript, it would be helpful for the readers if it was briefly explained how secondary structure is inferred from DMS reactivity, as this technique is not broadly used.

It is not objective to refer to the Lan et al. model of RNA structure as "high quality" given the limitations of their experimental approach (low MOI, asynchronous infection, DMS-only, no long-range interactions) and the lack of external validation of the structure of the genome they propose.

I removed “high-quality” from the abstract. Since a result of the paper is that secondary structure correlates  with synonymous substitution rates, this is an observation that can be used to retrospectively compare the  quality of secondary structure models in this respect. I updated the manuscript to include such a  comparison, and did not find a large difference between secondary structure models (Results lines  110–122). I added a discussion of how multiple data sources can potentially be integrated to more  accurately predict the impact of a substitution of viral fitness.

I have also added a brief discussion of constraints on how much we can confidently infer from these  experiments given limitations of the experimental approach. I note that DMS and SHAPE data provide  information that can be combined to make a stronger model, and that predictions can be rapidly tested  given observations by Gout (Symonds?) et al that  in  vitro  substitution rates correlate with those observed  during the pandemic (Discussion lines 195–201).

Mutational fitness from Bloom & Neher was derived throughout the pandemic, much of which came from a period with the most active surveillance (Delta / Omicron waves). Consequently, these viruses differ from the WA1 strain used by Lan et al. far more than the 3 nt differences between lineage A and B that the author refers to. The following sentence should therefore be revised to avoid misleading the reader:

"Additionally, note that DMS data was obtained in experiments using the WA1 strain in Lineage A, which differs from the more common Lineage B at 3 positions and could have different secondary structure."

Revised:

“Additionally, note that DMS data was obtained in experiments using the WA1 strain in Lineage A,  which differs from the more common Lineage B at 3 positions and could have different secondary  structure. Furthermore, mutational fitness is estimated from the phylogenetic tree of published  sequences (the public UShER tree (Turakhia et al., 2021) additionally curated to filter likely artifacts  such as branches with numerous reversions) that are typically far more divergent and subsequently  will have somewhat different secondary structures. Since the dataset used for mutational fitness  aggregates data across viral clades, my analysis will not capture secondary structure variation  between clades or indels and masked sites that were not considered in that analysis (Bloom and  Neher, 2023).”

To determine the extent to which the results depend on the single RNA structure model, it would be informative "turn the crank again" on the analysis with one of the other RNA structure datasets for SARS-CoV-2 (though most other datasets suffer from similar problems of asynchronicity of infection).

I have added comparisons when the Lan  et al  secondary  structure model is replaced by one of two others  derived from SHAPE data as described above. Also, I conducted preliminary comparisons of underlying  DMS and SHAPE reactivity data as described above, but I opted not to include these in the revised  manuscript given that methods different beyond the chemical probe used. I also discuss how multiple data  sources can potentially be integrated to more accurately predict the impact of a substitution of viral fitness.

In Figure 1 it would be helpful to add the values of the unpaired/basepaired ratios in the plot for clarity.

Furthermore, a similar analysis using the substitution frequency, which strengthens the conclusions, is mentioned in the text, however, it is not shown. It could be shown as part of Figure 1, or as a supplementary figure.

This was a good suggestion since numbers around 1 are not perceived as being very significant. I added  the ratio of median unpaired:paired rates to Figure 1, updated the corresponding manuscript text and the  figure caption, and note that the numbers are somewhat changed from the first version of my manuscript  because of updating to use the most up-to-date mutational fitness estimates.

It is not clear how the two constants were calculated to obtain the "adjusted mutational fitness". It could be shown as part of Figure 2, or as a supplementary figure.

I added dashed lines and arrows to Figure 2 showing median paired/unpaired mutational fitnesses and the  adjustment made to normalize to the overall median. I also added Figure S3 showing this for synonymous  substitutions, where it is more clear given the lower fraction of mutations with substantial fitness impacts.

Minor comments

Statements like "the current fast-growing lineage JN.1.7" never age well... please revise to state the period of time to which this refers.

Revised:

“…lineage JN.1.7, which had over 20% global prevalence in Spring 2024…”

Also, I checked the list of mutations and the examples given remain in the top 15 ranked basepaired,  non-synonymous C→U mutations (BA.2-defining C26060U is added to the list, but I did not update to  include this). It replaces C9246U, which was not mentioned in the first version of the manuscript.

Similarly, please provide context for the reader in the phrase: "This was one mutation that characterized the B.1.177 lineage" (e.g. add its early reference as "EU1" and that it predominated in Europe in autumn 2020, prior to the emergence of the Alpha variant).

Revised to add detail:

This was one of the mutations that characterized the B.1.177 lineage. This lineage, also known as  EU1, characterized a majority of sequences in Spain in summer 2020 and eventually in several  other countries in Europe prior to the emergence of the Alpha variant. However, it was unclear  whether or this lineage had higher fitness than other lineages or if A222V specifically conferred a  fitness advantage.

"massive sequencing of SARS-CoV-2" - the meaning of the word "massive" is unclear. Revise.

Revised  “…millions of patient SARS-CoV-2 sequences published during the pandemic…”

Author response:

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

We were pleased that many of the critical comments of the reviewers have allowed us to improve our manuscript. In addition to revise the originally submitted figures, we performed new experiments (e.g. new Fig.2, Fig.3, Fig.4, and Fig.6) and revised the manuscript substantially following the reviewers’ comments and suggestions to our initial submission. A point-by-point response to the reviewers’ critiques are summarized below, and new supportive data are provided in this revised manuscript. Per the Reviewers’ comments and revisions, we revised the title to be “Cold induces brain region-selective cell activity-dependent lipid metabolism”. 

Reviewer #1:

Strengths:

A strength of the study is trying to better understand how metabolism in the brain is a dynamic process, much like how it has been viewed in other organs. The authors also use a creative approach to measuring in vivo lipid peroxidation via delivery of a BD-C11 sensor through a cannula to the region in conjunction with fiber photometry to measure fluorescence changes deep in the brain.

We thank the Reviewer so much for the positive comments on this interesting study on metabolism in the brain.

Weaknesses:

One weakness was many of the experiments were done in a manner that could not distinguish between the contributions of neurons and glial cells, limiting the extent of conclusions that could be made. While this is not easily doable for all experiments, it can be done for some. For example, the Fos experiments in Figure 3 would be more conclusive if done with the labeling of neuronal nuclei with NeuN, as glial cells can also express Fos. To similarly show more conclusively that neurons are being activated during cold exposure, the calcium imaging experiments in Figure S3 can be done with cold exposure. 

We agreed with the Reviewers’ comments. We revised the original Figure 3 (new Figure 6) and Figure S3 (new Figure S4). Our data show that cold increased Fos-positive cells in the PVH (Figure 6) and increased neuronal Ca2+ signals (new Figure S4). As it is difficult to exclude the involvements of astrocytes in the cold-induced lipid metabolism, and to address this reviewer’s questions, we revised the title and the text with replacing “neuronal” with “‘cell” activity, and we concluded that cold induced lipid metabolism depending on “cell activity” instead of “neuronal activity”. Studying cell type-specific contributions to the cold-induced effects on lipid metabolism will require many efforts beyond the scope of this study, to which we assumed that both neurons and glial cells contribute.

Additionally, many experiments are only done with the minimal three animals required for statistics and could be more robust with additional animals included.  

We thank this reviewer for the comments. We added the sample sizes accordingly in this revised manuscript.

Another weakness is that the authors do not address whether manipulating lipid droplet accumulation or lipid peroxidation has any effect on PVH function (e.g. does it change neuronal activity in the region?).

We thank this reviewer for bringing up this interesting point. The focus of this study was to examine how cold modulates lipid metabolism in the brain, while it is another interesting project studying how brain lipid metabolism (e.g. manipulating LD accumulation or lipid peroxidation) modulates neuronal activity, which however will require many efforts beyond the scope of this study. Manipulating LD or peroxidation would affect multiple cellular signaling pathways and physiological experimental conditions need to be developed. However, to address this reviewer’s questions, we performed preliminary studies with treating brain slices with the lipid peroxidation inhibitor a-TP and recorded PVH neurons, but did not observe differences in firing rates in a-TPtreated brain slices and controls (Data not shown).  

Reviewer #2:

Strengths:

A set of relatively novel and interesting observations. Creative use of several in vivo sensors and techniques.

We thank the Reviewer so much for the positive comments on our studies in both concept and techniques. 

Weaknesses:  

(1) The physiological relevance of lipolysis and thermogenesis genes in the PVH. The authors need to provide quantitative and substantial characterizations of lipid metabolism in the brain beyond a panel of qPCRs, especially considering these genes are likely expressed at very low levels. mRNA and protein level quantification of genes in Fig 1, in direct comparison to BAT/iWAT, should be provided. Besides bulk mRNA/protein, IHC/ISH-based characterization should be added to confirm to cellular expression of these genes.

We agreed with the Reviewer’s comments and thank this reviewer for the constructive suggestions. To address this reviewer’s comments and suggestions, we performed additional experiments to verify cold-induced expressions of lipid lipolytic genes and proteins. For example, we stained ATGL and HSL in both neurons and astrocytes in the PVH. Matching with the increased gene expressions, cold increased protein expressions of ATGL (new Figure 2) and HSL (new Figure 3) in both neurons and astrocytes. We also performed western blots of p-HSL and HSL and observed that cold increased the expression level of p-HSL (new Figure 4). These new results support our conclusions and further demonstrate that cold increases lipid metabolism in the PVH.   

(2) The fiberphotometry work they cited (Chen 2022, Andersen 2023, Sun 2018) used well-established, genetically encoded neuropeptide sensors (e.g., GRABs). The authors need to first quantitatively demonstrate that adapting BD-C11 and EnzCheck for in vivo brain FP could effectively and accurately report peroxidation and lipolysis. For example, the sensitivity, dynamic range, and off-time should all be calibrated with mass spectrometry measurements before any conclusions can be made based on plots in Figures 4, 5, and 6. This is particularly important because the main hypothesis heavily relies on this unvalidated technique.

We thank this reviewer’s comments. Fiber photometry has been well demonstrated to detect fluorescent-labelled biomolecules in my laboratory and other labs, as indicated in the above stated publications. In this study, we combined photometry with the well commercially developed and validated lipid metabolic fluorescent-labelled biomarkers to monitor lipid metabolic dynamics in vivo. We indeed verified this approach in both brain (this study) and peripheral adipose tissues (another project). Particularly, our data in this study show that lipid peroxidation inhibitor a-TP blocked the cold-induced lipid peroxidation signals (Fig. 7A-C) and the pan-lipase inhibitor DEUP blocked the cold-induced lipolytic signals (Fig. 8A-C). These results demonstrate that the signals detected by photometry indeed reflect lipid peroxidation and lipolysis respectively in the brain. Meanwhile, we agreed with the reviewer’s suggestions on mass spectrometry measurements, while it is not feasible for us to perform the spectrometry in the brain in vivo at this moment.       

(3) Generally, the histology data need significant improvement. It was not convincing, for example, in Figure 3, how the Fos+ neurons can be quantified based on the poor IF images where most red signals were not in the neurons. 

We thank this reviewer for this comment. We performed additional experiments to add sample size and presented high quality images. 

(4) The hypothesis regarding the direct role of brain temperature in cold-induced lipid metabolism is puzzling. From the introduction and discussion, the authors seem to suggest that there are direct brain temperature changes in responses to cold, which could be quite striking. However, this was not supported by any data or experiments. The authors should consolidate their ideas and update a coherent hypothesis based on the actual data presented in the manuscript. 

We thank this reviewer for bringing up this comment and constructive suggestions. To make this study more concise on the cold-induced lipid metabolism, we removed the statements related to the brain temperature.

Reviewer #1 (Recommendations For The Authors):

An additional minor weakness is that the authors are redundant in their discussion, sometimes repeating sections from the introduction (e.g. this line in the discussion "Evidence shows that the brain's energy expenditure efficiency largely depends on the temperature (Yu et al., 2012), and temperature gradients between different brain regions exist (Anderson and Moser, 1995; Delgado and Hanai, 1966; Hayward and Baker, 1968; McElligott and Melzak, 1967; Moser and Mathiesen, 1996; Thornton, 2003)"). 

We thank the Reviewer for these comments. We revised the text following the suggestions accordingly and removed the statements and references related to brain temperatures.

Author response:

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

Reviewer #1 (Public review):

Summary: 

IPF is a disease lacking regressive therapies which has a poor prognosis, and so new therapies are needed. This ambitious phase 1 study builds on the authors' 2024 experience in Sci Tran Med with positive results with autologous transplantation of P63 progenitor cells in patients with COPD. The current study suggests that P63+ progenitor cell therapy is safe in patients with ILD. The authors attribute this to the acquisition of cells from a healthy upper lobe site, removed from the lung fibrosis. There are currently no cell-based therapies for ILD and in this regard the study is novel with important potential for clinical impact if validated in Phase 2 and 3 clinical trials. 

Strengths: 

This study addresses the need for an effective therapy for interstitial lung disease. It offers good evidence that the cells used for therapy are safe. In so doing it addresses a concern that some P63+ progenitor cells may be proinflammatory and harmful, as has been raised in the literature (articles which suggested some P63+ cells can promote honeycombing fibrosis; references 26 &35). The authors attribute the safety they observed (without proof) to the high HOPX expression of administered cells (a marker found in normal Type 1 AECs. The totality of the RNASeq suggests the cloned cells are not fibrogenic. They also offer exploratory data suggesting a relationship between clone roundness and PFT parameters (and a negative association between patient age and clone roundness). 

We thank the reviewer for the important comments.

Weaknesses: 

The authors can conclude they can isolate, clone, expand, and administer P63+ progenitor cells safely; but with the small sample size and lack of a placebo group, no efficacy should be implied.

We thank the reviewer for the suggestion and agree that we should be more cautious to discuss the efficacy of current study. 

Specific points: 

(1) The authors acknowledge most study weaknesses including the lack of a placebo group and the concurrent COVID-19 in half the subjects (the high-dose subjects). They indicate a phase 2 trial is underway to address these issues. 

N/A

(2) The authors suggest an efficacy signal on pages 18 (improvement in 2 subjects' CT scans) and 21 (improvement in DLCO) but with such a small phase 1 study and such small increases in DLCO (+5.4%) the authors should refrain from this temptation (understandable as it is). 

We believe that exploring potential efficacy signal is also one aim of this study. All these efficacy endpoint analyses had been planned in prior to the start of clinical trials (as registered in ClinicalTrial.gov) and the data need be analyzed anyhow.

(3) Likewise most CT scans were unchanged and those that improved were in the mid-dose group (albeit DLCO improved in the 2 patients whose CT scans improved). 

Yes, it is.

(4) The authors note an impressive 58m increase in 6MWTD in the high-dose group but again there is no placebo group, and the low-dose group has no net change in 6MWTD at 24 weeks. 

Yes.

(5) I also raise the question of the enrollment criteria in which 5 patients had essentially normal DLCO/VA values. In addition there is no discussion as to whether the transplanted stem cells are retained or exert benefit by a paracrine mechanism (which is the norm for cell-based therapies).

Thank you for your detailed feedback.  The enrollment criteria are based on DLCO instead of DLCO/VA. And we would like to further discuss the possible benefit by paracrine mechanism in the revised manuscript.

Recommendations for the authors: 

(1) Four of the enrolled subjects had normal DLCO/VA (% of predicted) (>90% of predicted). This raises questions about the severity of their illness see: Table 1: Subjects 103, 105, 112, and 204 have DLCO/VA % predicted >90% of predicted and would appear not to qualify for the study. While technically enrollment criteria for DLCO are satisfied, DLCO/VA is an equally valid measure of ILD severity, and these 4 cases seem very mild. 

Thank you for your detailed feedback. Yes, the current inclusion criteria is based on DLCO but not DLCO/VA.  And we believe improvement of DLCO and DLCO/VA is both meaningful. In future trial, we will consider DLCO/VA as inclusion criteria as well.

(2) The authors state "Resolution of honeycomb lesion was also observed in patients of higher dose groups". This appears inaccurate as only 2 subjects in the study showed CT improvement and they were not in the highest dose group. This statement is an overreach for a Phase 1 study and should be removed from the abstract and more balance inserted in the text. The phase 2 study they are doing will answer these questions. 

Thank you. We changed our statement about efficacy in the abstract part.

a) Under exclusion criteria: More detail is required as to what defines "subjects who cannot tolerate cell therapy". 

Those patients cannot tolerate previous cell therapy, for example mesenchymal stem cell transplantation, would not be included in the current trial.

b) Figure S6 is important and should be in the main manuscript. This Figure shows that many (6) subjects had COVID at some trial measurement time points. This is an unfortunate confounder for efficacy signals (but efficacy is not the point of this study). Second, Figure 6 (in my view) shows little efficacy signal, which is a reminder to the authors that efficacy should not be implied in a study that was not powered to detect efficacy. 

We agreed that the efficacy should be discussed very carefully.

(3) Figure S3: It appears at some does there is a significant rise in monocytes (1M cells) and neutrophils (3 M cells). 

Thank you for your reasonable concerns regarding the safety of the treatment. The monocyte counts in the S3 patients, even after an increase, remains within the reference range, and therefore we consider this elevation to be clinically meaningless. One patient exhibited a significant increase in neutrophils at 24 weeks, which was attributed to a grade II adverse event, acute bronchitis, which was unrelated to cell therapy. The symptoms resolved within three days following treatment with appropriate medication.

(4) Figure 3: I wonder about the statistical significance of the 6MWD. Was this done by repeat measure ANOVA? The analysis suggests a p=0.08 but all error bars between low and high dose overlap and the biggest difference is at 24 weeks, and that appears to be labelled as not significant.

Thank you for your kind reminding. The 6MWD result with a p-value of 0.008 was derived to compare the improvement in 6MWD at the 24-week time point versus baseline within the higher group. Therefore, a paired t-test was used for this analysis. In the revised version, we label them more clearly.

Reviewer #2 (Public review):

Summary: 

This manuscript describes a first-in-human clinical trial of autologous stem cells to address IPF. The significance of this study is underscored by the limited efficacy of standard-of-care anti-fibrotic therapies and increasing knowledge of the role p63+ stem cells in lung regeneration in ARDS. While models of acute lung injury and p63+ stem cells have benefited from widespread and dynamic DAD and immune cell remodeling of damaged tissue, a key question in chronic lung disease is whether such cells could contribute to the remodeling of lung tissue that may be devoid of acute and dynamic injury. A second question is whether normal regions of the lung in an otherwise diseased organ can be identified as a source of "normal" p63+ stem cells, and how to assess these stem cells given recently identified p63+ stem cell variants emerging in chronic lung diseases including IPF. Lastly, questions of feasibility, safety, and efficacy need to be explored to set the foundation for autologous transplants to meet the huge need in chronic lung disease. The authors have addressed each of these questions to different extents in this initial study, which has yielded important if incomplete information for many of them. 

Strengths: 

As with a previous study from this group regarding autologous stem cell transplants for COPD (Ref. 24), they have shown that the stem cells they propagate do not form colonies in soft agar or cancers in these patients. While a full assessment of adverse events was confounded by a wave of Covid19 infections in the study participants, aside from brief fevers it appears these transplants are tolerated by these patients. 

We thank the reviewer for the important comments.

Weaknesses: 

The source of stem cells for these autologous transplants is generally bronchoscopic biopsies/brushings from 5th-generation bronchi. Although stem cells have been cloned and characterized from nasal, tracheal, and distal airway biopsies, the systematic cloning and analysis of p63+ stem cells across the bronchial generations is less clear. For instance, p63+ stem cells from the nasal and tracheal mucosa appear committed to upper airway epithelia marked by 90% ciliated cells and 10% goblet cells (Kumar et al., 2011. Ref. 14). In contrast, p63+ stem cells from distal lung differentiate to epithelia replete with Club, AT2, and AT1 markers. The spectrum of p63+ stem cells in the normal bronchi of any generation is less studied. In the present study, cells are obtained by bronchoscopy from 3-5 generation bronchi and expanded by in vitro propagation. Single-cell RNA-seq identifies three clusters they refer to as C1, C2, and C3, with the major C1 cluster said to have characteristics of airway basal cells and C2 possibly the same cells in states of proliferation. Perhaps the most immediate question raised by these data is the nature of the C1/C2 cells. Whereas they are clearly p63/Krt5+ cells as are other stem cells of the airways, do they display differentiation character of "upper airway" marked by ciliated/goblet cell differentiation or those of the lung marked by AT2 and AT1 fates? This could be readily determined by 3-D differentiation in so-called airliquid interface cultures pioneered by cystic fibrosis investigators and should be done as it would directly address the validity of the sourcing protocol for autologous cells for these transplants. This would more clearly link the present study with a previous study from the same investigators (Shi et al., 2019, Ref. 9) whereby distal airway stem cells mitigated fibrosis in the murine bleomycin model. The authors should also provide methods by which the autologous cells are propagated in vitro as these could impact the quality and fate of the progenitor cells prior to transplantation. 

We totally agree that the sub-population of the progenitor cells should be further analyzed. We would try this in the revised manuscript. And the methods to expand P63+ lung progenitor cells have been described in full details by Frank McKeon/Wa Xian group (Rao, et.al., STAR Protocols, 2020), which is adapted to pharmaceutical-grade technology patented by Regend Therapeutics, Ltd.

The authors should also make a more concerted effort to compare Clusters 1, 2, and 3 with the variant stem cell identified in IPF (Wang et al., 2023, Ref. 27). While some of the markers are consistent with this variant stem cell population, others are not. A more detailed informatics analysis of normal stem cells of the airways and any variants reported could clarify whether the bronchial source of autologous stem cells is the best route to these transplants.  

We thank for reviewer for the good suggestion and would like to make more detailed comparison in the revised manuscript.

Other than these issues the authors should be commended for these firstin-human trials for this important condition.

Thank you so much for the kind compliment.

Recommendations for the authors: 

Described in the review text but the authors need to be clear about how they propagated autologous stem cells in vitro.

(1) Perhaps the most immediate question raised by these data is the nature of the C1/C2 cells. Whereas they are clearly p63/Krt5+ cells as are other stem cells of the airways, do they display differentiation character of "upper airway" marked by ciliated/goblet cell differentiation or those of the lung marked by AT2 and AT1 fates?

The differentiation potential of the P63+/KRT5+ basal progenitor cells have been analyzed in multiple previous literatures, which are mentioned in the revised introduction part. Basically, the human P63+ progenitor cells can differentiate into airway epithelial cells in the airway area, while give rise to immature, but functional AT1 cells in alveolar area.

(2) The authors should also provide methods by which the autologous cells are propagated in vitro as these could impact the quality and fate of the progenitor cells prior to transplantation.

The methods to expand P63+ lung progenitor cells have been described in full details by Frank McKeon/Wa Xian group (Rao, et.al., STAR Protocols, 2020), which is adapted to pharmaceutical-grade technology patented by Regend Therapeutics, Ltd.

(3) A more detailed informatics analysis of normal stem cells of the airways and any variants reported could clarify whether the bronchial source of autologous stem cells is the best route to these transplants.

We thank the reviewer for the kind suggestion and have included the comparative analysis in revised Figure S2.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this manuscript, authors have investigated the effects of JNK inhibition on sucrose-induced metabolic dysfunction in rats. They used multi-tissue network analysis to study the effects of the JNK inhibitor JNK-IN-5A on metabolic dysfunction associated with excessive sucrose consumption. Their results show that JNK inhibition reduces triglyceride accumulation and inflammation in the liver and adipose tissues while promoting metabolic adaptations in skeletal muscle. The study provides new insights into how JNK inhibition can potentially treat metabolic dysfunction-associated fatty liver disease (MAFLD) by modulating inter-tissue communication and metabolic processes.

Strengths:

The study has several notable strengths:

Comprehensive Multi-Tissue Analysis: The research provides a thorough multi-tissue evaluation, examining the effects of JNK inhibition across key metabolically active tissues, including the liver, visceral white adipose tissue, skeletal muscle, and brain. This comprehensive approach offers valuable insights into the systemic effects of JNK inhibition and its potential in treating MAFLD.

Robust Use of Systems Biology: The study employs advanced systems biology techniques, including transcriptomic analysis and genome-scale metabolic modeling, to uncover the molecular mechanisms underlying JNK inhibition. This integrative approach strengthens the evidence supporting the role of JNK inhibitors in modulating metabolic pathways linked to MAFLD.

Potential Therapeutic Insights: By demonstrating the effects of JNK inhibition on both hepatic and extrahepatic tissues, the study offers promising therapeutic insights into how JNK inhibitors could be used to mitigate metabolic dysfunction associated with excessive sucrose Behavioral and Metabolic Correlation: The inclusion of behavioral tests alongside metabolic assessments provides a more holistic view of the treatment's effects, allowing for a better understanding of the broader physiological implications of JNK inhibition.

Weaknesses:

While the study provides a comprehensive evaluation of JNK inhibitors in mitigating MAFLD conditions, addressing the following points will enhance the manuscript's quality:

The authors should explicitly mention and provide a detailed list of metabolites affected by sucrose and JNK inhibition treatment that have been previously associated with MAFLD conditions. This will better contextualize the findings within the broader field of metabolic disease research.

We fully agreed on this constructive suggestion to improve our understanding of the metabolic effect of JNK inhibition under sucrose overconsumption. While technical limitations made it challenging to directly analyze metabolites in the current study, we employed genome-scale metabolic modeling—a robust approach for studying metabolism—to predict the metabolic pathways potentially impacted by the interventions (Fig. 7 and Data S8). Additionally, as part of this revision, we conducted an extensive literature review to identify metabolites previously reported to be affected by sucrose consumption in MAFLD rodent models and MASLD patients. A detailed summary of these metabolites is now presented in attached Table 1 and several of these metabolites have been incorporated into the revised results section (Lines 308-314) to support some of the predicted metabolic activities.

“Some of the predicted metabolic changes align with previous findings in rodents subjected to sucrose overconsumption. For example, Öztürk et al. reported altered tryptophan metabolism, including decreased serum levels of kynurenic acid and kynurenine, in rats consuming 10% sucrose in drinking water. Similarly, increased triglyceride-bound oleate, palmitate, and stearate were observed in the livers of rats fed a 10% sucrose solution, indicating JNK-IN-5A treatment may regulate lipid metabolism by modulating these metabolic activities.”

It is important to note, however, that data on metabolites specifically affected by JNK inhibition in MASLD contexts remains lacking in the literature. The predicted metabolites and associated metabolic pathways in the current study could provide a starting point for such exploration in future studies. We have emphasized this in the revised manuscript and highlighted the need for further studies to explore these mechanisms in greater detail.

Author response table 1.

Metabolites associated with sucrose overconsumption in MASLD.

The limitations of the study should be clearly stated, particularly the lack of evidence on the effects of chronic JNK inhibitor treatment and potential off-target effects. Addressing these concerns will offer a more balanced perspective on the therapeutic potential of JNK inhibition.

Thank you for this constructive comment. We have acknowledged limitations of the current study in Discussion section (Lines 397-406) of the revised manuscript:

“Nevertheless, several limitations warrant consideration. First, while we observed transcriptional adaptations in skeletal muscle tissue following treatment, the exact molecular mechanisms underlying these changes and their roles in skeletal muscle function and systemic metabolic homeostasis remain unclear. Further investigation is warranted to elucidate the muscle-specific effects of JNK inhibition. Second, our study did not investigate the dosedependent or potential off-target effects of JNK-IN-5A, particularly its activity on other members of the kinase family and associated signaling pathways. Lastly, the long-term effects of JNKIN-5A administration remain unexplored. Understanding its prolonged impact across different stages of MAFLD, including advanced MASH, is crucial for assessing the full therapeutic potential of JNK inhibition in the treatment of MAFLD.“

The potential risks of using JNK inhibitors in non-MAFLD conditions should be highlighted, with a clear distinction made between the preventive and curative effects of these therapies in mitigating MAFLD conditions. This will ensure the therapeutic implications are properly framed.

Thank you for this insightful suggestion. The potential risks of using JNK inhibitors in nonMAFLD conditions have been considered and are now highlighted in Lines 369-390 of the revised discussion

“Although overactivated JNK activity presents an attractive opportunity to combat MAFLD, inhibition of JNK presents substantial challenges and potential risks due to its broad and multifaceted roles in many cellular processes. One key challenge is the dual role of JNK signaling (Lamb et al., 2003). For instance, long-term JNK inhibition may disrupt liver regeneration, as JNK plays a critical role in liver repair by regulating hepatocyte proliferation and survival following injury or stress (Papa and Bubici, 2018). In HCC, it has been reported that JNK acts as both a tumor promoter, driving inflammation, fibrosis, and metabolic dysregulation, and a tumor suppressor, facilitating apoptosis and cell cycle arrest in damaged hepatocytes. Its inhibition, therefore, carries the risk of inadvertently promoting tumor progression under certain conditions (Seki et al., 2012). Furthermore, the differential roles of JNK isoforms (JNK1, JNK2, JNK3) and a lack of specificity of JNK inhibitors present another layer of complexity. Given these challenges, while our study demonstrated the potential of JNK-IN-5A in mitigating early metabolic dysfunction in the liver and adipose tissues, JNK targeting strategies should be carefully tailored to the disease stage under investigation. For curative approaches targeting advanced MAFLD, such as MASH, future studies are warranted to address considerations related to dosing, tissue specificity, and the long-term effects.”

The statistical analysis section could be strengthened by providing a justification for the chosen statistical tests and discussing the study's power. Additionally, a more detailed breakdown of the behavioral test results and their implications would be beneficial for the overall conclusions of the study.

We would like to thank you for this constructive suggestion. In this study, differences among more than two groups were tested using ANOVA or Kruskal-Wallis test based on the normality testing (Shapiro–Wilk test) on the data (continuous variables from different measurements). Pairwise comparisons, were performed using Tukey’s post hoc test following ANOVA or Dunn’s multiple comparisons post hoc test following the Kruskal-Wallis test, as appropriate. 

The study used 11 animals per group, a group size widely used in preclinical animal research [13]. To evaluate the power of this study design to detect group differences, we conducted a power analysis using G*Power 3.1 software [14], with ANOVA used as an example. The power analysis revealed the following:

- For a small effect size (partial eta.sq = 0.01), the power was 7.5% at 𝑝<0.05.

- For a medium effect size (partial eta.sq = 0.06), the power was 23.7% at 𝑝<0.05.

- For a large effect size (partial eta.sq = 0.14), the power is 55.4% at 𝑝<0.05

Bonapersona et al. reported that the median statistical power in animal studies is often between 15–22% [15], the achieved power of the current study design is within the range observed in most exploratory animal research. However, we acknowledge that the power for detecting smaller effects within groups is limited, which is also a common challenge in animal research due to ethical considerations on increasing sample sizes.

As suggested, we’ve revised the ‘Statistical Analysis’ and ‘Result’ sections to improve clarity:

“Statistical Analysis:

Data were shown as mean ± standard deviation (SD), unless stated otherwise. The assumption of normality for continuous variables from behavior test, biometric measurements, and plasm biochemistry was determined using the Shapiro–Wilk test. Differences among multiple groups were tested by ANOVA or, for data that were not normally distributed, the non-parametric Kruskal-Wallis test. Pairwise comparisons were performed using Tukey’s post hoc test following the ANOVA or Dunn’s multiple comparisons post hoc test following the Kruskal-Wallis test, as appropriate. The Jaccard index was used to evaluate the similarity and diversity of two gene sets, and a  hypergeometric test was used to test the significance of their overlap. All results were considered statistically significant at p < 0.05, unless stated otherwise.”

Behavior tests (Lines 150-157):

“We found no significant differences among groups in retention latencies, a measure of learning and memory abilities in passive avoidance test (Data S3). Additionally, the locomotor activity test was used to analyze behaviors such as locomotion, anxiety, and depression in rat. No significant differences were observed among groups in stereotypical movements, ambulatory activity, rearing, resting percentage, and distance travelled (Data S4). Similarly, the elevated plus maze test (Walf and Frye, 2007), an assay for assessing anxiety-like behavior in rodents, showed that rats in all groups had comparable open-arm entries and durations (Data S5). Collectively, the behavior tests indicate the JNK-IN-5A-treated rats exhibit no evidence of anxiety and behavior disorders.”

Reviewer #2 (Public review):

Summary:

Excessive sucrose is a possible initial factor for the development of metabolic dysfunctionassociated fatty liver disease (MAFLD). To investigate the possibility that intervention with JNK inhibitor could lead to the treatment of metabolic dysfunction caused by excessive sucrose intake, the authors performed multi-organ transcriptomics analysis (liver, visceral fat (vWAT), skeletal muscle, and brain) in a rat model of MAFLD induced by sucrose overtake (+ a selective JNK2 and JNK3 inhibitor (JNK-IN-5A) treatment). Their data suggested that changes in gene expression in the vWAT as well as in the liver contribute to the pathogenesis of their MAFLD model and revealed that the JNK inhibitor has a cross-organ therapeutic effect on it.

Strengths:

(1)It has been previously reported that inhibition of JNK signaling can contribute to the prevention of hepatic steatosis (HS) and related metabolic syndrome in other models, but the role of JNK signaling in the metabolic disruption caused by excessive intake of sucrose, a possible initial factor for the development of MAFLD, has not been well understood, and the authors have addressed this point.

(2)This study is also important because pharmacological therapy for MAFLD has not yet been established.

(3)By obtaining transcriptomic data in multiple organs and comprehensively analyzing the data using gene co-expression network (GCN) analysis and genome-scale metabolic models (GEM), the authors showed the multi-organ interaction in not only in the pathology of MAFLD caused by excessive sucrose intake but also in the treatment effects by JNK-IN-5A.

(4) Since JNK signaling has diverse physiological functions in many organs, the authors effectively assessed possible side effects with a view to the clinical application of JNK-IN-5A.

Weaknesses:

(1) The metabolic process activities were evaluated using RNA-seq results in Figure 7, but direct data such as metabolite measurements are lacking.

Thank you for these valuable insights. We fully agree that direct metabolite measurements would provide a deeper understanding of the metabolic impact of sucrose overconsumption and JNK-IN-5A administration. Unfortunately, due to technical limitations, we were unable to directly measure metabolites in this study. To address this, we supported our genome-scale metabolic modeling predictions with an extensive literature review, which is summarized in attached Table 1. This table highlights key metabolites and associated metabolic pathways that have been previously associated with sucrose overconsumption in MAFLD contexts. We incorporated some of these metabolites into the revised results section (Lines 308–314) to demonstrate the consistency between our predicted metabolic changes and experimental findings from the literature. For instance, studies have reported altered tryptophan metabolism, including decreased serum kynurenic acid and kynurenine levels, as well as increased triglyceride-bound oleate, palmitate, and stearate in sucrose-fed rodents. These findings align with our predictions of altered metabolic activities in fatty acid oxidation, fatty acid synthesis, and tryptophan metabolism.

(2) There is a lack of consistency in the data between JNK-IN-5A_D1 and _D2, and there is no sufficient data-based explanation for why the effects observed in D1 were inconsistent in the D2 samples.

Thank you for raising this important point regarding the differences between the two dosages. As this was not the primary focus of the current study and we do not have sufficient data to fully explain these observations. Our speculation is that this may arise from pharmacokinetic differences associated with the dosing of this small molecule inhibitor, including potential saturation of transport mechanisms, alter tissue distribution, or off-target effects.

(3) Although it is valuable that the authors were able to suggest the possibility of JNK inhibitor as a therapeutic strategy for MAFLD, the evaluation of the therapeutic effect was limited to the evaluation of plasma TG, LDH, and gene expression changes. As there was no evaluation of liver tissue images, it is unclear what changes were brought about in the liver by the excessive sucrose intake and the treatment with JNK-IN-5A.

We acknowledge that the lack of histological evaluations may limit to having a complete picture of the interventions' effects. However, as you noted, our transcriptional and systems-wide investigation across multiple tissues provides novel and significant insights into the molecular and systemic impacts of JNK-IN-5A treatment.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

(1) It would be useful to explain why the authors conducted their research using female rats but not male rats.

Thank you for raising this insightful point. We chose female rats for the current study was based on several considerations. 1) Previous research has demonstrated that female rats exhibit metabolic dysfunction (e.g., hypertriglyceridemia, liver steatosis, insulin resistance) in response to dietary factors, such as high-sucrose feeding [16-19]. These metabolic characteristics made them an appropriate model for assessing the in vivo effects of JNK inhibition under high-sucrose conditions. 2) It is also reported that female rats show resilience to high-sucrose-induced metabolic dysfunction due to the protective effects of estrogen [8], we aimed to determine whether JNK inhibition could provide therapeutic benefits in this context. This allows us to evaluate the effect of JNK inhibition even in metabolically advantaged groups. 3) Our results from the tolerance test (Fig. 2a) indicated that female rats displayed more fluctuating variation to JNK-IN-5A administration. This variation allowed us to evaluate how JNK inhibition influences metabolic outcomes in a sex that is more responsive to the intervention. Nonetheless, we emphasize the importance of future studies involving male rats to better understand sex-specific responses to JNK inhibition and to provide more comprehensive guidance for the development of JNK-targeting therapies in MAFLD treatment.

(2) Figure 2C shows that JNK-IN-5A administration reduces the mRNA levels of Mapk8 and Mapk9 in the liver and the SkM. It would be useful to provide the authors' insight into the data. 

In the liver, the data in Fig. 2c in original submission and the attached Fig. 1 show that sucrose feeding induces opposite alterations in the mRNA expression of Mapk8 (Jnk1, increased, log2FC_{SucrosevsControl}= 0.02) and Mapk9 (Jnk2, decreased, log2FC_{SucrosevsControl}= -0.43), though these changes do not reach statistical significance. JNK-IN-5A administration reverses these effects, significantly decreasing Mapk8 expression (log2FC_{Sucrose+JNK_D1vsSucrose}= -0.37) while increasing Mapk9 expression (log2FC_{Sucrose+JNK_D1vsSucrose}= 0.42). This suggests potential differential yet compensatory roles of these two isoforms in regulating JNK activity during these interventions in the liver, keeping in line with the findings from Jnk1- and/or Jnk2-specific knockout studies [20, 21]. Additionally, emerging evidence indicates that Jnk1 plays a major role in diet-induced liver fibrosis and metabolic dysfunction [22-25]. Therefore, the reduced Mapk8 expression following JNK-IN-5A administration may contribute to the observed improvements in liver metabolism.

Author response image 1.

The spearman correlation between expression levels of Mapk8

In skeletal muscle, the primary site for insulin-stimulated glucose uptake, insulin signaling is crucial for maintaining metabolic homeostasis [26]. Numerous studies have demonstrated that JNK activation promotes insulin resistance and targeting JNK might be a promising therapeutic strategy for the treatment of metabolic diseases associated with insulin resistance, such as MAFLD [24]. In our study, while sucrose overconsumption did not significantly alter the mRNA levels of JNK isoforms in this tissue, JNK-IN-5A at dosage 30 mg/kg/day administration significantly reduced the expression of both Jnk1 and Jnk2 as well as genes involved in insulin signaling (Fig. 5). This suggests a potential interplay between JNK inhibition and insulin signaling pathways in the skeletal muscle, where inhibition of JNK activity may improve insulin sensitivity by modulating these pathways. However, it is also crucial  to investigate the longterm effects of JNK-IN-5A administration and its broader impact on many other physiological processes regulated by the JNK pathway. These aspects will be a focus of our future studies.

(3) The notations a and b in Figure S5 are missing.  

Thank you for this constructive comment. We have corrected this in the revised figure S5.

(4) Data S13 described in the figure legend for Figure 7 (lines 630 and 632) seems a mistake and should be Data S8.

(5) The notations a, b, and c in Figure 7 are incorrect. The figure legend for Figure 7a doesn't seem to match the figure contents.

We appreciate your attention to details regarding Fig. 7. We have corrected the reference and the figure legend in revised Fig. 7.

Reference

(1) Fujii, A., et al., Sucrose Solution Ingestion Exacerbates DinitrofluorobenzeneInduced Allergic Contact Dermatitis in Rats. Nutrients, 2024. 16(12).

(2) Sun, S., et al., High sucrose diet-induced dysbiosis of gut microbiota promotes fatty liver and hyperlipidemia in rats. J Nutr Biochem, 2021. 93: p. 108621.

(3) Qi, S., et al., Inositol and taurine ameliorate abnormal liver lipid metabolism induced by high sucrose intake. Food Bioscience, 2024. 60: p. 104368.

(4) Ramos-Romero, S., et al., The Buckwheat Iminosugar d-Fagomine Attenuates Sucrose-Induced Steatosis and Hypertension in Rats. Mol Nutr Food Res, 2020. 64(1): p. e1900564.

(5) Ortiz, S.R. and M.S. Field, Sucrose Intake Elevates Erythritol in Plasma and Urine in Male Mice. J Nutr, 2023. 153(7): p. 1889-1902.

(6) Beckmann, M., et al., Changes in the human plasma and urinary metabolome associated with acute dietary exposure to sucrose and the identification of potential biomarkers of sucrose intake. Mol Nutr Food Res, 2016. 60(2): p. 444-57.

(7) He, X., et al., High Fat Diet and High Sucrose Intake Divergently Induce Dysregulation of Glucose Homeostasis through Distinct Gut Microbiota-Derived Bile Acid Metabolism in Mice. J Agric Food Chem, 2024. 72(1): p. 230-244.

(8) Stephenson, E.J., et al., Chronic intake of high dietary sucrose induces sexually dimorphic metabolic adaptations in mouse liver and adipose tissue. Nat Commun, 2022. 13(1): p. 6062.

(9) Mock, K., et al., High-fructose corn syrup-55 consumption alters hepatic lipid metabolism and promotes triglyceride accumulation. J Nutr Biochem, 2017. 39: p. 32-39.

(10) Eryavuz Onmaz, D. and B. Ozturk, Altered Kynurenine Pathway Metabolism in Rats Fed Added Sugars. Genel Tıp Dergisi, 2022. 32(5): p. 525-529.

(11) Gariani, K., et al., Eliciting the mitochondrial unfolded protein response by nicotinamide adenine dinucleotide repletion reverses fatty liver disease in mice. Hepatology, 2016. 63(4): p. 1190-204.

(12) Togo, J., et al., Impact of dietary sucrose on adiposity and glucose homeostasis in C57BL/6J mice depends on mode of ingestion: liquid or solid. Mol Metab, 2019. 27: p. 22-32.

(13) Arifin, W.N. and W.M. Zahiruddin, Sample Size Calculation in Animal Studies Using Resource Equation Approach. Malays J Med Sci, 2017. 24(5): p. 101-105.

(14) Faul, F., et al., G*Power 3: a flexible statistical power analysis program for the social, behavioral, and biomedical sciences. Behav Res Methods, 2007. 39(2): p. 175-91.

(15) Bonapersona, V., et al., Increasing the statistical power of animal experiments with historical control data. Nat Neurosci, 2021. 24(4): p. 470-477.

(16) Kendig, M.D., et al., Metabolic EYects of Access to Sucrose Drink in Female Rats and Transmission of Some EYects to Their OYspring. PLoS One, 2015. 10(7): p. e0131107.

(17) Harris, R.B.S., Source of dietary sucrose influences development of leptin resistance in male and female rats. Am J Physiol Regul Integr Comp Physiol, 2018. 314(4): p. R598-R610.

(18) Velasco, M., et al., Sexual dimorphism in insulin resistance in a metabolic syndrome rat model. Endocr Connect, 2020. 9(9): p. 890-902.

(19) Maniam, J., C.P. Antoniadis, and M.J. Morris, The eYect of early-life stress and chronic high-sucrose diet on metabolic outcomes in female rats. Stress, 2015. 18(5): p. 524-37.

(20) Singh, R., et al., DiYerential eYects of JNK1 and JNK2 inhibition on murine steatohepatitis and insulin resistance. Hepatology, 2009. 49(1): p. 87-96.

(21) Sabapathy, K., et al., Distinct roles for JNK1 and JNK2 in regulating JNK activity and c-Jun-dependent cell proliferation. Mol Cell, 2004. 15(5): p. 713-25.

(22) Zhao, G., et al., Jnk1 in murine hepatic stellate cells is a crucial mediator of liver fibrogenesis. Gut, 2014. 63(7): p. 1159-72.

(23) Czaja, M.J., JNK regulation of hepatic manifestations of the metabolic syndrome. Trends Endocrinol Metab, 2010. 21(12): p. 707-13.

(24) Solinas, G. and B. Becattini, JNK at the crossroad of obesity, insulin resistance, and cell stress response. Mol Metab, 2017. 6(2): p. 174-184.

(25) Schattenberg, J.M., et al., JNK1 but not JNK2 promotes the development of steatohepatitis in mice. Hepatology, 2006. 43(1): p. 163-72.

(26) Sylow, L., et al., The many actions of insulin in skeletal muscle, the paramount tissue determining glycemia. Cell Metab, 2021. 33(4): p. 758-780.

Author response:

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

Public Reviews

Reviewer #1 (Public review)

Weaknesses: 

The main weakness of the manuscript is that to a large degree, one of its main conclusions (MAP symmetry underlies differences in regenerative capacity) relies mainly on a correlation, without firmly establishing a causal link. However, this weakness is relatively minor because (1) it is partially addressed with the Spastin KO and (2) there isn't a trivial way to show a causal relationship in this case.

We thank Reviewer #1 for their positive assessment of our manuscript. To further strengthen the claim that MAP asymmetry underlies differences in regenerative capacity, we could investigate the effect of depleting other MAPs that lose asymmetry after conditioning lesion (CRMP5 and katanin). One would expect that similarly to spastin, this would disrupt the physiological asymmetry of DRG axons and impair axon regeneration. We further discussed this issue in the revised version of the manuscript (page 17, line 381).

Reviewer #2 (Public review)

Weaknesses:

In order for the method to be used it needs to be better described. For instance what proportion of neurons develop just two axonal branches, one of which is different? How selective are the researchers in finding appropriate neurons?

We thank Reviewer #2 for their positive assessment of our manuscript. As suggested, we included further methodological details on the in vitro system in the revised version of the manuscript. We have previously evaluated the percentage of DRG neurons exhibiting different morphologies in our cultures: multipolar (4±1%), bipolar, (35±8%) bell-shaped (17±5%), and pseudo-unipolar neurons (43±3%). This was included in the revised manuscript on Figure 1B and page 5, line 107.  All the pseudo-unipolar neurons analysed had distinct axonal branches in terms of diameter and microtubule dynamics. For imaging purposes, we selected pseudounipolar neurons with axons unobstructed from other cells or neurites within a distance of at least 20–30 μm from the bifurcation point, to ensure optimal imaging. In the case of laser axotomy experiments, this distance was increased to 100–200 μm to ensure clear analysis of regeneration. These selection criteria is now detailed in the Methods (page 19, line 417, and page 21, line 474).

Reviewer #3 (Public review):

(1) Weaknesses:

While some of the data are compelling, experimental evidence only partially supports the main claims. In its current form, the study is primarily descriptive and lacks convincing mechanistic insights. It misses important controls and further validation using 3D in vitro models.

We recognize the importance of further exploring the contribution of other MAPs to microtubule asymmetry and regenerative capacity of DRG axons. In future work, we plan to investigate this issue using knockout mice for katanin and CRMP5. Regarding the mechanisms underlying the differential localization of proteins in DRG axons, we performed in-situ hybridization to evaluate the availability of axonal mRNA but no differences were found between central and peripheral DRG axons (Figure 4 – figure supplement 2). To address whether differences in protein transport exist, we attempted to transduce DRG neurons with GFP-tagged spastin both in vitro and in vivo. However, these experiments were inconclusive as very low levels of spastin-GFP were detected. We are actively optimizing these approaches and will address this challenge in future studies. These points were further discussed in the revised manuscript (page 15, line 330 and page 17, line 381).

(2) Given the heterogeneity of dorsal root ganglion (DRG) neurons, it is unclear whether the in vitro model described in this study can be applied to all major classes of DRG neurons. 

We acknowledge the diversity of DRG neurons and agree that assessing the presence

of different DRG subtypes in our culture system will enrich its future use. Despite this heterogeneity, we focused on DRG neuron features that are common to all subtypes i.e, pseudo-unipolarization and higher regenerative capacity of peripheral branches. This point was addressed on page 14, line 309 of the revised manuscript.

(3) Also unclear is the inconsistency with embryonic DRG cultures with embryonic (E)16 from rats and E13 from mice (spastin knockout and wild-type controls). 

Given our previous experience in establishing DRG neuron cultures from E16 Wistar rats and E13 C57BL/6 mice, these developmental stages are equivalent, yielding cultures of DRG neurons with similar percentages of different morphologies. Of note, in our colonies, gestation length is ~19 days in C57BL/6 mice (background of the spastin knockout line) and ~22 days in Wistar Han rats. This was further clarified in the Methods (page 18, line 404).

(4) Furthermore, the authors stated (line 393) that only a small subset of cultured DRG neurons exhibited a pseudo-unipolar morphology. The authors should include the percentage of the neurons that exhibit a pseudo-unipolar morphology.

We have previously evaluated the percentage of DRG neurons exhibiting different morphologies in our cultures: multipolar (4±1%), bipolar, (35±8%) bell-shaped (17±5%), and pseudo-unipolar neurons (43±3%). This was included in the revised manuscript on Figure 1B and on page 5, line 107. In line 393, we referred specifically to an experimental setup where DRG neuron transduction was done, and 30 transduced neurons were randomly selected for longitudinal imaging. From these, the number of viable pseudo-unipolar DRG neurons was limited by both the random nature of viral transduction and light-induced toxicity throughout continuous imaging over seven consecutive days at hourly intervals. This was clarified in the revised manuscript (page 20, line 438).

(5) The significance of studying microtubule polymerization to DRG asymmetry in vitro is questionable, especially considering the model's validity. The authors might consider eliminating the in vitro data and instead focus on characterizing DRG asymmetry in vivo both before and after a conditioning lesion. If the authors choose to retain the in vitro data, classifying the central and peripheral-like branches in cultured DRG neurons will require further in-depth characterization. Additional validation should be performed in adult DRG neuron cultures not aged in vitro.

The in vitro system here presented reliably reproduces several key features of DRG neurons observed in vivo, including asymmetry in axon diameter, regenerative capacity, axonal transport, and microtubule dynamics. Of note, most studies in the field have been done using multipolar DRG neurons that do not recapitulate in vivo morphology and asymmetries. Thus, the current in vitro model serves as a versatile tool for advancing our understanding of DRG biology and associated diseases. This system is particularly suited to study axon regeneration asymmetries, and enables the investigation of mechanisms occurring at the stem axon bifurcation, such as asymmetric protein transport and microtubule dynamics, which are challenging to examine in vivo due to the length of the stem axon and the difficulty of locating the DRG T-junction. It will be important to optimize similar cultures using adult DRG neurons. However, this comes with challenges, such as lower cell viability. This is the case with multiple other neuron types for which the vast majority of cultures are obtained from embryonic tissue. These concerns were addressed in the revised version of the manuscript (page 13, line 296 and page 14 line 302).

(6) The comparison of asymmetry associated with a regenerative response between in vitro and in vivo paradigms has significant limitations due to the nature of the in vitro culture system. When cultured in isolation, DRG neurons fail to form functional connections with appropriate postsynaptic target neurons (the central branch) or to differentiate the peripheral domains associated with the innervation of target organs. Rather than growing neurons on a flat, hard surface like glass, more physiologically relevant substrates and/or culturing conditions should be considered. This approach could help eliminate potential artifacts caused by plating adult DRG neurons on a flat surface. Additionally, the authors should consider replicating their findings in a 3D culture model or using dorsal root ganglia explants, where both centrally and peripherally projecting axons are present.

We agree that a more sophisticated system, such as a compartmentalized culture, holds great potential for future research. In this respect, we are currently engaged in developing such models. A compartmentalized system would enable the separation of three compartments: central nervous system neurons, DRG neurons, and peripheral targets. While previous efforts to create compartmentalized DRG cultures have been reported (e.g., PMID: 11275274 and PMID: 37578145), these systems have not demonstrated the development of pseudo-unipolar morphology. Incorporating non-neuronal DRG cells into the DRG neuron compartment, may successfully support the development of a pseudo-unipolar morphology. 

We also recognize the importance of dimensionality in fostering pseudo-unipolar morphology. Of note, our model provides a 3D-like environment, as DRG glial cells are continuously replicating over the 21 days in culture. In relation to DRG explants, we attempted their use but encountered limitations with confocal microscopy as the axial resolution was insufficient to resolve processes at the DRG T-junction or within individual branches. The above issues are now discussed in the revised manuscript (page 14, line 312).

(7) Panels 5H-J require additional processing with astrocyte markers to accurately define the lesion borders. Furthermore, including a lower magnification would facilitate a direct comparison of the lesion site. 

In our study, we relied on the alignment of nuclei to delineate the lesion site as in our accumulated experience, this provides an accurate definition of the lesion boarder. Outside the lesion, the nuclei are well-aligned, while at the lesion site, they become randomly distributed. Additionally, CTB staining further supports the identification of the rostral boarder of the lesion, as most injured central DRG axons stop their growth at the injury site. This was further detailed in the Methods of the revised manuscript (page 32, line 730).

(8) The use of cholera toxin subunit B (CTB) to trace dorsal column sensory axons is prone to misinterpretation, as the tracer accumulates at the axon's tip. This limitation makes it extremely challenging to distinguish between regenerating and degenerating axons.

While alternative methods to trace or label regenerating axons exist, CTB is a wellestablished and widely used tracer for central sensory projections, as shown in different studies (PMID: 22681683, PMID: 26831088 and PMID: 33349630). Regarding the concern of possiblebCTB labeling in degenerating axons, we believe this is unlikely to be the case in our system, as in spinal cord injury controls, CTB-positive axons are nearly absent. Also, as regeneration was investigated six weeks after injury, axon degeneration has most likely already occurred as shown in (PMID: 15821747 and PMID: 25937174).

Recommendations for the authors: 

Reviewer #1:

(1) Figure 1 can be improved by adding a quantification of the fraction of neurons at each stage as a function of time.

We have updated Figure 1 to include the quantification of the percentages of different DRG neuron morphologies at DIV21 (Figure 1B), which corresponds to the stage at which all in vitro experiments were conducted.

(2) Figure 3A: why are retrograde transport events not shown?

Retrograde transport events are not displayed as results did not reach statistical significance.

(3) Figure 3 and 4: Combine the quantifications of with/without lesion, such that not only the differences between branches are apparent, but also the differences induced in each branch by the lesion.

As requested, only combined quantifications of microtubule dynamics for naive and conditioning lesion are provided in the revised version of Figure 3 (Figures 3H and 3K), to highlight both branch-specific differences and lesion-induced changes. However, for Figure 4, as the western blots for naive and conditioning lesion were performed on separate gels, it is unfeasible to combine their quantification.

(4) Figure 5: does spastin KO lead to a difference in the "MAP signature" of each branch? Also, if in addition to MAPs there are other known molecules (and an antibody is available) that show differential localization to peripheral/central branches, it would be nice to check if this asymmetry is also lost in spastin KO.

Evaluating the MAP signature in DRG axons from spastin KO mice will be important to explore in future experiments. Despite some scattered reports in the literature, our study is the first to identify a distinct protein signature of central and peripheral DRG axons. This is especially relevant in the case of Tau, as irrespective of the experimental conditions, its levels are always increased in the peripheral DRG axon.

Reviewer #2:

(1) Please provide a more complete description of the culture method. Do all neurons develop two asymmetric branches or just a few, and how are they selected? Does the timing of the events in vitro correspond with what is happening to the neurons in embryos?

We have included the percentages of the various DRG neuron morphologies at DIV21 in the revised manuscript (Figure 1B and on page 5, line 107). Additionally, a more detailed description of the culture method is now provided in the Methods, including the criteria used to select pseudo-unipolar neurons (page 19, line 417, and page 21, line 474). 

Regarding the timing of events, upon DRG dissociation, neurons reinitiate polarization, taking 21 days to reach approximately 40% pseudo-unipolar morphology. A similar percentage is reached at E16.5 during rat development in vivo (PMID: 8729965).

(2) Are the neurons and their branches resting on the glia? Is there any relation to the presence of glia and the type of growth that is seen?

Yes, neurons and their branches rest on glia. This is required for DRG pseudounipolarization. In future studies, we plan to further investigate neuron-extrinsic mechanisms leading pseudo-unipolarization, and to identify the specific glial cell type(s) needed throughout this process. This is now discussed in the revised manuscript (page 14, line 306).

(3) Is it possible to trace microtubules so as to see whether the microtubules of the two branches mix, or whether they remain separate all the way to the cell bodies?

We used DRG neurons transduced with EB3-GFP, to examine microtubule polymerization at the T-junction through live imaging. This revealed a high continuum of polymerization from the stem axon to the central-like axon (Figure 4 – figure supplement 2D-G). To further determine whether microtubules from both branches mix or remain separate, alternative techniques such as FIB-SEM could be performed. This point is now further discussed in the revised manuscript (page 16, line 352).

(4) Using the term MAPs would lead readers to expect to see an analysis of different levels of MAP1, MAP2, etc. It would be interesting to see this if the authors have done it, but it is not necessary for the paper.

We assessed the expression of MAP2 via western blot in DRG peripheral and central axons and no differences were found. This is now referred to in the Discussion (pages 15, line 327).

(5) The regeneration experiments on the spastin knockouts are complicated by the lesion being in CNS tissue, which introduces various issues. Is there a difference in regeneration after dorsal root crush?

We have not yet examined whether regeneration differs after dorsal root crush in the spastin knockout model. However, this presents an interesting question, as Schwann cells in the dorsal root, may support regeneration of central DRG axons.  

Reviewer #3:

The authors stated that the normality of the datasets was tested using the Shapiro-Wilk or D'Agostino-Pearson omnibus normality test. Given the low sample size (n=4) for some of the experiments presented (e.g., Figure 3B), it is not clear how normality was assessed which justifies the use of parametric tests.

We followed GraphPad’s recommendations for selecting the appropriate normality test (https://www.graphpad.com/support/faqid/959/). The D'Agostino-Pearson omnibus K2 test, recommended for its versatility, was used when sample size was 8 or more. For smaller sample sizes (n < 8), we used the Shapiro-Wilk test, which is also widely used in biological research and can be employed with datasets of at least 3 values. These tests guided our decision-making regarding the use of parametric or non-parametric statistical tests.

Author response:

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

Public Reviews:

Reviewer #2 (Public Review):

The manuscript by Zhang et al. explores the effect of autophagy regulator ATG6 on NPR1-mediated immunity. The authors propose that ATG6 directly interacts with NPR1 in the nucleus to increase its stability and promote NPR1-dependent immune gene expression and pathogen resistance. This novel role of ATG6 is proposed to be independent of its role in autophagy in the cytoplasm. The authors demonstrate through biochemical analysis that ATG6 interacts with NPR1 in yeast and very weakly in vitro. They further demonstrate using overexpression transgenic plants that in the presence of ATG6-mcherry the stability of NPR1-GFP and its nuclear pool is increased.

Comments on latest version:

The term "invasion" has to be replaced with infection, as it doesn't have much meaning to this particular study. I already explained this point in the first review, but authors did not address it throughout the manuscript.

Thank you for your constructive feedback. We have taken your suggestion into account and replaced "invasion" with "infection" in the revised manuscript (Lines 44,45,99,100,298,341,387,415,461,463,464,1002).

In fig. 1e there's no statistical analysis. How can one show measurements from multiple samples without statistical analysis? All the data points have to be shown in the graph and statistics performed. In the arg6-npr1 and snrk-npr1 pairs no nuclear marker is included. How can one know where the nucleus is, particularly in such poor quality low res. images? The nucleus marker has to be included in this analysis and shown. This is an important aspect of the study as nuclear localization of ATG6 is proposed to be essential for its new function.

Thank you for bringing this to our attention. We conducted the BIFC experiments again using nls-mCherry transgenic tobacco, which yielded clearer images. The results clearly demonstrate that ATG6 interacts with NPR1 in both the cytoplasm and nucleus. YFP signaling in the nucleus co-localizes with nls-mCherry (a nuclear localization mark). SnRK2.8 was employed as a positive control for NPR1 interaction." Relative fluorescence intensity of YFP were analyzed using image J software, n = 15 independent images were analyzed to quantify YFP fluorescence. All data points are displayed in the image, and we also conducted a Student's t-test analysis. We have incorporated these results into the revised manuscript (Fig 1d and e).

Co-localization provided in the fig. S2 cannot complement this analysis, particularly since no cytoplasmic fraction is present for NPR1-GFP in fig. S2.

Thank you for your observation. We repeated the experiment and confirmed that NPR1 and ATG6 co-localize in both the nucleus and cytoplasm. The image in Figure S2 has been updated accordingly.

In the alignment in fig 2c, it is not explained what are the species the atg6 is taken from. The predicted NLS has to be shown in the context of either the entire protein sequence alignment or at least individual domain alignment with the indication of conserved residues (consensus). They have to include more species in the analysis, instead of including 3 proteins from a single species. Also, the predicted NLS in atg6 doesn't really have the classical type architecture, which might be an indication that it is a weak NLS, consistent with the fact that the protein has significant cytoplasmic accumulation. They also need to provide the NLS prediction cut-off score, as this parameter is a measure of NLS strength.

Line 150: the NLS sequence "FLKEKKKKK" is a wrong sequence.

Thank you for your suggestion. In both plants and animals, proteins are transported to the nucleus via specific nuclear localization signals (NLSs), which are typically characterized by short stretches of basic amino acids (Dingwall and Laskey, 1991, Raikhel, 1992, Nigg, 1997). Following your recommendation, we re-predicted potential NLS sequences in the ATG6 protein using NLSExplorer (http://www.csbio.sjtu.edu.cn/bioinf/NLSExplorer). Although we did not identify a classical monopartite NLS, we discovered a bipartite NLS similar to the consensus bipartite sequence (KRX_(10-12)K(KR)(KR)) (Kosugi et al., 2009)in the carboxy-terminal region (475-517 aa) of ATG6, with a cut-off score of 2.6. These findings are consistent with substantial accumulation of ATG6 in the cytoplasm and minimal accumulation in the nucleus. Additionally, our comparison of ATG6 C-terminal sequences across several species, including Microthlaspi erraticum, Capsella rubella, Brassica carinata, Camelina sativa, Theobroma cacao, Brassica rapa, Eutrema salsugineum, Raphanus sativus, Hirschfeldia incana and Brassica napus, sequence comparison indicates that this bipartite NLS is relatively conserved. We have incorporated these results into the revised manuscript (lines 450-160).

In fig. 3d no explanation for the error bars is included, and what type of statistical analysis is performed is not explained.

Thank you for bringing this to our attention. In Figure 3d, a Student's t-test was conducted to analyze the data. The mean and standard deviation were calculated from three biological replicates, and the relevant description has been included in the figure notes.

Reference

Dingwall, C. and Laskey, R.A. (1991) Nuclear targeting sequences--a consensus? Trends Biochem Sci, 16, 478-481.

Kosugi, S., Hasebe, M., Matsumura, N., Takashima, H., Miyamoto-Sato, E., Tomita, M. and Yanagawa, H. (2009) Six classes of nuclear localization signals specific to different binding grooves of importin alpha. J Biol Chem, 284, 478-485.

Nigg, E.A. (1997) Nucleocytoplasmic transport: signals, mechanisms and regulation. Nature, 386, 779-787.

Raikhel, N. (1992) Nuclear targeting in plants. Plant Physiol, 100, 1627-1632.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Weaknesses:

However, given that S1P is upstream NF-κB signaling, it is unclear if it offers conceptual innovations as compared to previous studies from the same team (Palazzo et al. 2020; 2022, 2023)

We find distinct differences between the impacts of S1P- and NFkB-signaling on glial activation, neuronal differentiation of the progeny of MGPCs and neuronal survival in damaged retinas. In the current study we demonstrate that 2 consecutive daily intravitreal injections of S1P selectively activated mTor (pS6) and Jak/Stat3 (pStat3), but not MAPK (pERK1/2) signaling in Müller glia.  Further, inhibition of S1P synthesis (SPHK1 inhibitor) decreased ATF3, mTor (pS6) and pSmad1/5/9 levels in activated Müller glia in damaged retinas. Inhibition of NFkB-signaling in damaged chick retinas did not impact the above-mentioned cell signaling pathways (Palazzo et al., 2020). Thus, S1P-signaling impacts cell signaling pathways in MG that are distinct from NFκB, but we cannot exclude the possibility of cross-talk between NFkB and these pathways. Further, inhibition of NFκB-signaling potently decreases numbers of dying cells and increases numbers of surviving ganglion cells (Palazzo et al 2020). Consistent with these findings, a TNF orthologue, which presumably activates NFκB-signaling, exacerbates cell death in damage retinas (Palazzo et al., 2020). By contrast, 5 different drugs targeting S1P-signaling had no effect on numbers of dying cells and only one S1PR1 inhibitor modestly decreased numbers of dying cells (current study). Although two different inhibitors of NFkB-signaling suppressed the proliferation of microglia in damaged retinas (Palazzo et al., 2020), all of the S1P-targeting drugs had no effect upon the proliferation of microglia (current study). In addition, inhibition of NFκB does not influence the neurogenic potential of MGPCs in damaged chick retinas (Palazzo et al., 2020), whereas inhibition of S1P receptors (S1PR1 and S1PR3) and inhibition of S1P synthesis (SPHK1) significantly increased the differentiation of amacrine-like neurons in damaged retinas (current study). Collectively, in comparison to the effects of pro-inflammatory cytokines and NFκB-signaling, our current findings indicate that S1P-signaling through S1PR1 and S1PR3 in Müller glia has distinct effects upon cell signaling pathways, neuronal regeneration and cell survival in damaged retinas. We will revise text in the Discussion (pages 33-34) to better highlight these important distinctions between NFκB- and S1P-signaling.

Reviewer #2 (Public review):

Weaknesses:

The methodology is not very clean. A number of drugs (inhibitors/ antagonists/agonists signal modulators) are used to modulate S1P expression or signaling in the retina without evidence that these drugs are reaching the target cells. No alternative evaluation if the drugs, in fact, are effective. The drug solubility in the vehicle and in the vitreous is not provided, and how did they decide on using a single dose of each drug to have the optimal expected effect on the S1P pathway?

Müller glia are the predominant retinal cell type that expresses S1P receptors. Consistent with these patterns of expression, we report Müller glia-specific effects of different agonists and antagonists that increase or decrease S1P-signaling. Since we compare cell-level changes within contralateral eyes wherein one retina is exposed to vehicle and the other is exposed to vehicle plus drug, it seems highly probable that the drugs are eliciting effects upon the Müller glia. It is possible, but very unlikely, that the responses we observed could have resulted from drugs acting on extra-retinal tissues, which might secondarily release factors that elicit cellular responses in Müller glia. However, this seems unlikely given the distinct patterns of expression for different S1P receptors in Müller glia, and the outcomes of inhibiting Sphk1 or S1P lyase on retinal levels of S1P.

For example, we provide evidence that S1PR1 and S1PR3 expression is predominant in Müller glia in the chick retina using single cell-RNA sequencing and fluorescence in situ hybridization (FISH). Thus, we expect that S1PR1/3-targeting small molecule inhibitors to directly act on Müller glia, which is consistent with our read-outs of cell signaling with injections of S1P in undamaged retinas. We show that SPHK1 and SGPL1, which encode the enzymes that synthesize or degrade S1P, are expressed by different retinal cell types, including the Müller glia. The efficacy of the drugs that target SPHK1 and SGPL1 was assessed by measuring levels of S1P in the retina. By using liquid chromatography and tandem mass spectroscopy (LC-MS/MS), we provide data that inhibition of S1P synthesis (inhibition of SPHK1) significantly decreased levels of S1P in normal retinas, whereas inhibition of S1P degradation (inhibition of SGPL1) increased levels of S1P in damaged retinas (Fig. 5).  These data suggest that the SPHK1 inhibitor and the SGPL1 inhibitor specifically act at the intended target to influence retinal levels of S1P.  Further, inhibition of SPHK1 (to decrease levels S1P) results in decreased levels of ATF3, pS6 (mTor) and pSMAD1/5/9 in Müller glia, consistent with the notion that reduced levels of S1P in the retina impacts signaling at Müller glia. Finally, we find similar cellular responses to chemically different agonists or antagonists, and we find opposite cellular responses to agonists and antagonists, which are expected to be complimentary if the drugs are specifically acting at the intended targets in the retina. We will revise the Discussion to better address caveats and concerns regarding the actions and specificity of different drugs within the retina following intravitreal delivery.

We will provide the drug solubility specifications and estimates of the initial maximum dose per eye for each drug. For chick eyes between P7 and P14, these estimates will assume a volume of about 100 ul of liquid vitreous, 800 ul gel vitreous and an average eye weight of 0.9 grams. We will revise Table 1 (pharmacological compounds) with ranges of reported in vivo ED50’s (mg/kg) for drugs and we will list the calculated initial maximum dose (mg/kg equivalent) per eye. Doses were chosen based on estimates of the initial maximum ocular dose that were within the range of reported ED50’s. However, as is the case for any in vivo model system, it is difficult to predict rates of drug diffusion out of the vitreous, how quickly the drugs are cleared from the entire eye, how much of the compound enters the retina, and how quickly the drug is cleared from the retina. Accordingly, we assessed drug specificity and sites of activation by relying upon readouts of cell signaling pathways that are parsed with patterns of expression of different S1P receptors and measurements of retinal levels of S1P following exposure to drugs targeted enzymes that synthesize or degrade S1P, as described above. 

Reviewer #1 (Recommendations for the authors):

I am wondering if Muller glia can be considered as fully differentiated at early postnatal stages as those used in this study. Is this mechanism operative in adult retinas? Could the authors perform studies in older animals, just to have the proof of principle that the proposed mechanism is retained.

Chickens are considered to be adult at about 4 months of age, when the females start laying eggs. Unfortunately, housing, maintenance, handling and experimentation on large adult chickens has proven to be challenging. Nevertheless, there is evidence that Muller glia reprogramming remains robust in mature chick retinas from the P1 through P30, but the zones of proliferation shift away from central retina and become increasingly confined to the retinal periphery (Fischer, 2005). MG “maturation” appears to occur in a central-to-peripheral gradient, much like the process of embryonic retinal differentiation, but a zone of regeneration-competent MG remains in the periphery during adolescent development (Fischer, 2005).

We have defined central vs peripheral retina in the Methods.

To partially address this question, we have generated a new supplemental Figure 6 showing (i) SPHK1 fluorescent in-situ labeling of central and peripheral regions at P10, and (ii) analysis of EdU+Sox2+ MGPCs in central versus regions treated with NMDA +/-S1PR1 inhibitor or NMDA+/- SPHK1 inhibitor. We find that patterns of S1PR1 transcription in the central region are similar to the peripheral region (not shown), and S1PR1 inhibition modestly increased numbers of MGPCs in central regions. Unlike the peripheral regions of retina, SPHK1 FISH signal in the central region remains low at 48 hours post-injury (supplemental Fig. 6). Additionally, we found that the SPHK1 inhibitor had no effect on numbers of proliferating MGPCs in the central regions of retina, whereas SPHK1 inhibitors stimulated proliferation of MGPCs in the periphery (Fig. 4). It is likely that mature MG in central retinal regions are not responsive to SPHK1 inhibition due to low levels of expression.

We have previously shown that Notch-related genes show unique patterns of expression in the central and peripheral retinas, and expression levels significantly change at P0, P7, and P21 (Ghai et al, 2010). We found that Notch inhibition reduced cell death and numbers of MGPCs in central regions but not peripheral regions. Recent sc-RNA sequencing analysis of murine macula and peripheral retinal regions has revealed interesting differences in NFKBIA/Z and NFIA expression, possibly indicating a difference in the early inflammatory transcriptional response to retinal damage (Zhang et al, 2024 biorxiv). We believe that spatial sequencing of peripheral “immature” and central “mature” chick Muller glia will be a useful tool in the future to reveal key differences in signaling pathway-related gene expression which confer a competence for regeneration in the periphery.

We have added text to the Results (pages 20-21) and Discussion (page 32) to address the S1P-signaling in central (mature MG) vs peripheral (immature MG) regions of the retina.

Minor points.

The abstract is difficult to follow and consists of a list of what activates or represses the formation of MGPC. Please rewrite the abstract to integrate information and provide a clearer message. Also, please include the species of study in the abstract and mention it again at the beginning of the results, at least.

We have rewritten the abstract to simplify and clarify our main points (p 2).

Lines 65-69. The sentence is unclear, perhaps there are words either missing or in excess and there is a need to check the spelling.

We have simplified this sentence to improve clarity and referenced our recently published review to support.

Lines 112-113. Please explain why " retinas were treated with saline, NMDA, or 2 or 3 doses insulin+FGF2 and the combination of NMDA and insulin+FGF2". There is a reference but readers will appreciate understanding right away why.

We have added a sentence to clarify the purpose of comparing gene expression patterns in MG and MGPCs in NMDA-damaged retinas versus retinas treated with insulin+FGF2.

Lines 223-257. This list of experiments is difficult to follow and perhaps should be summarized better. Somehow lines 257-261 say it all.

We have revised this section to clarify differences in outcomes between S1PR1/3 activators and inhibitors. We also stated the enzymatic functions of SPHK1 and SGPL1 to improve clarity.

Lines 392-441. Comparative expression analysis should be summarized as the message is somehow simple but the description is rather lengthy.

We have revised our comparative expression analyses to be more concise.

Reviewer #2 (Recommendations for the authors):

(1) Only a single dose of the drugs (inhibitor/ antagonists/agonists signal modulators) is used for each drug, as shown in Table 1. How do they know this is an effective dose?

We estimated the appropriate dose based on the initial maximum dose, which we based on the reported ED50 values for each drug. We have revised Table 1 to include this information.

(2) Most of the drugs appeared to be hydrophobic, but except for sphingosine and S1P, all are described to be injected with sterile saline. They must provide solubility characteristics of these drugs in solvents. For example, FTY720 is not water-soluble, which raises the question of all of their drugs' solubility, bioavailability to the cells of interest, and their effectivity in signal transduction in the retinal cells.

Some S1P-targeting compounds were delivered in 20% DMSO in saline to support the solubility of the different lipophillic small molecule agonists/antagonists. We have added information to the Methods to describe the use of DMSO to solubilize these drugs (p 6) in Table 1 and p 5. We have also revised Table 1 with ranges of reported ED50’s (mg/kg) for all drugs and listed the calculated initial maximum dose (mg/kg) per eye.

(3) Drugs were delivered to the vitreous chamber, but there was no information on how they would cross the inner limiting membrane to affect or modulate S1P metabolism in retinal MG or to bind the S1P receptors on MG or other retinal cell types.

All selected compounds are small-molecule drugs, many of which are structural analogues of sphingosine or S1P. These drugs would be classified as BDDCS Class II drugs, meaning they have low solubility but high cell permeability. Thus, it is highly probable that they diffuse across the ILM to act on S1P receptors on MG, but it is also likely that their bioavailability is more limited, requiring a higher dose, repeated doses, and the use of solubilizing agents. We have clarified our use of DMSO to solubilize these drugs (p 6) according to vendor recommendations (p 5). This information has been added to the Methods.

(4) Gene expression is a very dynamic process; without providing more evidence that the expression changes are the direct effect of the drug treatment, the conclusions made based on the gene expression profiles are not strong. Additional points:

We do not make assertions that changes in scRNA-seq expression profiles are the direct result of S1P-targetting drugs. We report significant changes in cellular expression profiles following NMDA-induced retinal damage or ablation of microglia. We feel that new experiments to assess the gene expression profiles of retinal cells that are directly downstream of the different S1P-targetting drugs is better suited for future studies.

(5) Please add in the introduction that there is only one sphingosine kinase in chicken, as no SPHK2 is known to be present.

We have added additional information regarding the expression of SPHK1 and SPHK2 genes in the chick genome (p 4).

(6) Fig 1d and in many other UMAP clusters, the low expressing genes are barely visible (Ex. 1d, S1PR2, and S1PR3); please extract them in separate UMAP clusters and provide them in supplements.

We have revised supplemental Figure 1 to include separate panels for each of the S1P-related gene.

(7) The Figure References for SPHK1 (Fig. 2e), SGPL1 (Fig. 2e), ASAH1 (Fig. 2f), CERS6 (Fig. 2f), and CERS5 (Fig. 2f) in the line # 124- 132 should belong to Figure 1, not Figure 2.

We have corrected these figure references (p 14).

(8) The description of the expression of zebrafish genes does not match the figures. For example, 'Similarly, sphk1 was detected in very few cells in the retina (Fig. 10j). By comparison, sphk2 was detected in a few bipolar cells and rod photoreceptors (Fig. 10j). Similar to patterns of expression seen in chick and human retinas, sgpl1 was detected in microglia and a few cells scattered among the different clusters of inner retinal neurons and rod photoreceptors (Fig. 10j)', the expression of these genes are not in very few or few scattered cells rather in many cells.

We have revised these statements to improve clarity and more accurately describe the data in Figure 10 (p 28).

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The authors employed a combinatorial CRISPR-Cas9 knockout screen to uncover synthetically lethal kinase genes that could play a role in drug resistance to kinase inhibitors in triple-negative breast cancer. The study successfully reveals FYN as a mediator of resistance to depletion and inhibition of various tyrosine kinases, notably EGFR, IGF-1R, and ABL, in triple-negative breast cancer cells and xenografts. Mechanistically, they demonstrate that KDM4 contributes to the upregulation of FYN and thereby is an important mediator of drug resistance. All together, these findings suggest FYN and KDM4A as potential targets for combination therapy with kinase inhibitors in triple-negative breast cancer. Moreover, the study may also have important implications for other cancer types and other inhibitors, as the authors suggest that FYN could be a general feature of drug-tolerant persister cells.

Strengths:

(1) The authors used a large combination matrix of druggable tyrosine kinase gene knockouts, enabling studying of co-dependence of kinase genes. This approach mitigates off-target effects typically associated with kinase inhibitors, enhancing the precision of the findings.

(2) The authors demonstrate the importance of FYN in drug resistance in multiple ways. They demonstrate synergistic interactions using both knockouts and inhibitors, while also revealing its transcriptional upregulation upon treatment, strengthening the conclusion that FYN plays a role in the resistance.

(3) The study extends its impact by demonstrating the potent in vivo efficacy of certain combination treatments, underscoring the clinical relevance of the identified strategies.

Weaknesses:

(1) The methods and figure legends are incomplete, posing a barrier to the reproducibility of the study and hindering a comprehensive understanding and accurate interpretation of the results.

We thank the reviewer for pointing this out. We tried adding as much detail in methods and figures legends as possible to maximize reproducibility and accuracy in interpreting our results as will be described for our responses for the recommendations for authors.

(2) The authors make use of a large quantity of public data (Fig. 2D/E, Fig. 3F/L/M, Fig 4C, Fig 5B/H/I), whereas it would have strengthened the paper to perform these experiments themselves. While some of this data would be hard to generate (e.g. patient data) other data could have been generated by the authors. The disadvantage of the use of public data is that it merely comprises associations, but does not have causal/functional results (e.g. FYN inhibition in the different cancer models with various drugs). Moreover, by cherry-picking the data from public sources, the context of these sources is not clear to the reader, and thus harder to interpret correctly. For example, it is not directly clear whether the upregulation of FYN in these models is a very selective event or whether it is part of a very large epigenetic re-programming, where other genes may be more critical. While some of the used data are from well-known curated databases, others are from individual papers that the reader should assess critically in order to interpret the data. Sometimes the public data was redundant, as the authors did do the experiments themselves (e.g. lung cancer drug-tolerant persisters), in this case, the public data could also be left out.

More importantly, the original sources are not properly cited. While the GEO accession numbers are shown in a supplementary table, the articles corresponding to this data should be cited in the main text, and preferably also in the figure legend, to clarify that this data is from public sources, which is now not always the case (e.g. line 224-226). If these original papers do already mention the upregulation of FYN, and the findings from the authors are thus not original, these findings should be discussed in the Discussion section instead of shown in the Results.

We welcome the reviewer’s concern. As reviewer pointed out, our analysis with FYN expression levels in multiple studies with drug tolerant cells may merely reflect association and not causal relationships. We had at least shown that FYN inhibition may reduce drug tolerance in TNBC and EGFR inhibitor treated lung cancer cells (figures 2H, 5E). The causal role of FYN in emergence of drug tolerance in other cancers treated with different drugs (such as irinotecan treated colon adenocarcinoma and gemcitabine treated pancreatic adenocarcinoma) may be beyond scope of this study. We made a brief discussion addressing this concern in lines 273-275.

We also added proper citations of the public data used in this study in main text and figure legends in lines 267-269. The GEO accession numbers are listed in supplementary table S2. Importantly, none of the referenced studies identified FYN as key factor in generating drug tolerant cells.

(3) The claim in the abstract (and discussion) that the study "highlights FYN as broadly applicable mediator of therapy resistance and persistence", is not sufficiently supported by the results. The current study only shows functional evidence for this for an EGFR, IGF1R, and Abl inhibitor in TNBC cells. Further, it demonstrates (to a limited extent) the role of FYN in gefitinib and osimertinib resistance (also EGFR inhibitors) in lung cancer cells. Thus, the causal evidence provided is only limited to a select subset of tyrosine kinase inhibitors in two cancer types. While the authors show associations between FYN and drug resistance in other cancer types and after other treatments, these associations are not solid evidence for a causal connection as mentioned in this statement. Epigenetic reprogramming causing drug resistance can be accompanied by altered gene expression of many genes, and the upregulation of FYN may be a consequence, but not a cause of the drug resistance. Therefore, the authors should be more cautious in making such statements about the broad applicability of FYN as a mediator of therapy resistance.

We fully agree with the reviewer’s concern that FYN upregulation is simply an association, and may not be the cause of drug tolerance and resistance. Therefore, to accurately convey our findings, we edited our manuscript in lines 34-36 in abstract to “FYN expression is associated with therapy resistance and persistence by demonstrating its upregulation in various experimental models of drug-tolerant persisters and residual disease following targeted therapy, chemotherapy, and radiotherapy” and lines 288-290 in discussion to “ Upregulation of FYN is a general feature of drug tolerant cancer cells, suggesting the association of FYN expression with drug resistance and tumor recurrence after treatment.” We hope this satisfies the reviewer.

(4) The rationale for picking and validating FYN as the main candidate gene over other genes such as FGFR2, FRK2, and TEK is not clear.

a. While gene pairs containing FGFR2 knockouts seemed to be equally effective as FYN gene pairs in the primary screening, these could not be validated in the validation experiment. It is unclear whether multiple individual or a pool of gRNAs were used for this validation, or whether only 1 gRNA sequence was picked per gene for this validation. If only 1 gRNA per gene was used, this likely would have resulted in variable knockout efficiencies. Moreover, the T7 endonuclease assay may not have been the best method to check knockout efficiency, as it only implies endonuclease activity around a gene (but not to the extent of indels that can cause frameshifts, such as by TIDE analysis, or extent of reduction in protein levels by western blot).

b. Moreover, FRK2 and TEK, also demonstrated many synergistic gene pairs in the primary screen. However, many of these gene pairs were not included in the validation screening. The selection criteria of candidate gene pairs for validation screening is not clear. Still, TEK-ABL2 was also validated as a strong hit in the validation screen. The authors should better explain the choice of FYN over other hits, and/or mention that TEK and FRK2 may also be important targets for combination treatment that can be further elucidated.

We thank the reviewer for improving our manuscript. We had concerns with the generalizability of FGFR2, FRK and TEK in TNBC as their expressions are very low in MDA-MB-231, nor were they enriched in TNBC compared to cancer cell lines of other subtypes. We added a brief comment on this concern in results section and discussion section (lines 150-154, figure S3). Although we acknowledge that the validations done in figure 2B is a result of only one guide RNA, with validations with pharmacological inhibition of FYN (figure 2F-I), we hope the reader and reviewer can be convinced with our key findings in synthetic lethality between FYN and other tyrosine kinases.

(5) On several occasions, the right controls (individual treatments, performed in parallel) are not included in the figures. The authors should include the responses to each of the single treatments, and/or better explain the normalization that might explain why the controls are not shown.

a. Figure 2G: The effect of PP2 treatment, without combined treatment, is not shown.

b. Figure 2H/3G: The effect of the knockouts on growth alone, compared to sgGFP, is not demonstrated. It is unclear whether the viability of knockouts is normalized to sgGFP, or to each untreated knockout.

c. Figure 2L: The effect of SB203580 as a single treatment is not shown.

We thank the reviewer for pointing this out. The data shown for all figures listed in these concerns were normalized by the changes in viability by pharmacological or genetic perturbations that synergized with TKIs (NVP-ADW742, gefitinib…etc.) used in the figures in the original manuscript. As reviewer had suggested, we newly added the effect of SB203580 and PP2 treatment on cell viability in supplementary figures S4A, S4K. SB203580 had no significant effect on cell viability, while PP2 treatment caused significant decrease in cell viability, which is expected as PP2 can inhibit activity of multiple Src family kinases. Regardless of the effect of SB203580 and PP2 on cell viability as single agent, it is evident that treatment of TKIs synergistically decreased cell viability in cancer cell lines. The change in viability by FYN or histone lysine demethylase knockout was also provided in newly added figure S4D and S6C. Notably, genetic ablation of FYN or histone lysine demethylases had modest, if any, influences on cell viability.

(6) The study examines the effects at a single, relatively late time point after treatment with inhibitors, without confirming the sequential impact on KDM4A and FYN. The proposed sequence of transcriptional upregulation of KDM4A followed by epigenetic modifications leading to FYN upregulation would be more compellingly supported by demonstrating a consecutive, rather than simultaneous, occurrence of these events. Furthermore, the protein level assessment at 48 hours (for RNA levels not clearly described), raises concerns about potential confounding factors. At this late time point, reduced cell viability due to the combination treatment could contribute to observed effects such as altered FYN expression and P38 MAPK phosphorylation, making it challenging to attribute these changes solely to the specific and selective reduction of FYN expression by KDM4A.

We thank the reviewer for pointing this out. We performed time course experiment for NVP-ADW742 treatment on MDA-MB-231 cells in our newly added figure 3E. Surprisingly, treatment of NVP-ADW742 increased KDM4A protein level within two hours. FYN protein accumulation followed KDM4A accumulation after 24 hours. This observation, with our chromatin immunoprecipitation data in figure 3O, provide evidence that FYN accumulation is a consequence of KDM4A accumulation and H3K9me3 demethylation upon TKI treatment. We newly discussed this data in results and discussion section in lines 214-216.

(7) The cut-off for considering interactions "synergistic" is quite low. The manual of the used "SynergyFinder" tool itself recommends values above >10 as synergistic and between -10 and 10 as additive ( https://synergyfinder.fimm.fi/synergy/synfin_docs/). Here, values between 5-10 are also considered synergistic. Caution should be taken when discussing those results. Showing the actual dose response (including responses to each single treatment) may be required to enable the reader to critically assess the synergy, along with its standard deviation.

We thank the reviewer for careful comments. We reanalyzed our data with SynergyFinder plus tool (Zheng, Genomics, Proteomics, and Bioinformatics 2022), which implements mathematical models distinct from SynergyFinder 3, for more faithful implementation of Bliss, Loewe independence models, and more critically, calculates statistical significance of the synergy. We provide updates synergy plots with statistics in figures 2F, 3J, and S4B. All drug combinations show statistically significant synergy (p<0.01). We also add raw data used to calculate synergy in figures 2F, 3J and S4B in supplementary dataset S2.

(8) As the effect size on Western blots is quite limited and sometimes accompanied by differences in loading control, these data should be further supported by quantifications of signal intensities of at least 3 biological replicates (e.g. especially Figure 3A/5A). The figure legends should also state how many independent experiments the blots are representative of.

We added quantifications for figure 3A and 5A for better depiction of our results. Figure legends were edited to indicate this is a representative of three independent experiments.

(9) While the article provides mechanistic insights into the likely upregulation of FYN by KDM4A, this constitutes only a fragment of the broader mechanism underlying drug resistance associated with FYN. The study falls short in investigating the causes of KDM4A upregulation and fails to explore the downstream effects (except for p38 MAPK phosphorylation, which may not be complete) of FYN upregulation that could potentially drive sustained cell proliferation and survival. These omissions limit the comprehensive understanding of the complete molecular pathway, and the discussion section does not address potential implications or pathways beyond the identified KDM4A-FYN axis. A more thorough exploration of these aspects would enhance the study's contribution to the field.

We welcome the reviewer’s careful concern. We agree our delineation of mechanisms underlying TKI resistance in TNBC involving KDM4 and FYN is far from complete. The increases in expression of histone demethylases were observed in cancers treated with different drugs. The mechanisms governing the increase in histone demethylase expression is not known and is beyond the scope of this paper. We newly added this in discussion section in lines 299-304.

(10) FYN has been implied in drug resistance previously, and other mechanisms of its upregulation, as well as downstream consequences, have been described previously. These were not evaluated in this paper, and are also not discussed in the discussion section. Moreover, the authors did not investigate whether any of the many other mechanisms of drug resistance to EGFR, IGF1R, and Abl inhibitors that have been described, could be related to FYN as well. A more comprehensive examination of existing literature and consideration of alternative or parallel mechanisms in the discussion would enhance the paper's contribution to understanding FYN's involvement in drug resistance.

FYN has been implicated in TKI resistance in CML cell lines (Irwin, Oncotarget, 2015). In this study, FYN is similarly transcriptionally upregulated in imatinib resistant CML, and this upregulation is dependent on EGR1 transcription factor. To address this concern, we generated EGR1 KO MDA-MB-231 cells and tested whether these cells retain the ability to accumulate FYN. Consistent with the previous study, imatinib treatment increased EGR1 protein level. However, EGR1 knockout did not influence FYN accumulation in MDA-MB-231 cells. EGR1 mediated accumulation of FYN may be context specific phenomenon to CML (Figure S5B). We newly discussed this result in result sections in lines 187-190. We also acknowledge that SRC family kinases are generally involved in drug resistance in many cancers. We discuss the recent findings regarding SRC family kinases in drug resistance in result section in lines 145-147 and discussion sections in lines 315-317.

Reviewer #2 (Public Review):

Summary:

Kim et al. conducted a study in which they selected 76 tyrosine kinases and performed CRISPR/Cas9 combinatorial screening to target 3003 genes in Triple-negative breast cancer (TNBC) cells. Their investigation revealed a significant correlation between the FYN gene and the proliferation and death of breast cancer cells. The authors demonstrated that depleting FYN and using FYN inhibitors, in combination with TKIs, synergistically suppressed the growth of breast cancer tumor cells. They observed that TKIs upregulate the levels of FYN and the histone demethylase family, particularly KDM4, promoting FYN expression. The authors further showed that KDM4 weakens the H3K9me3 mark in the FYN enhancer region, and the inhibitor QC6352 effectively inhibits this process, leading to a synergistic induction of apoptosis in breast cancer cells along with TKIs. Additionally, the authors discovered that FYN is upregulated in various drug-resistant cancer cells, and inhibitors targeting FYN, such as PP2, sensitize drug-resistant cells to EGFR inhibitors.

Strengths:

This study provides new insights into the roles and mechanisms of FYN and KDM4 in tumor cell resistance.

Weaknesses:

It is important to note that previous studies have also implicated FYN as a potential key factor in drug resistance of tumor cells, including breast cancer cells. While the current study is comprehensive and provides a rich dataset, certain experiments could be refined, and the logical structure could be more rigorous. For instance, the rationale behind selecting FYN, KDM4, and KDM4A as the focus of the study could be more thoroughly justified.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) The methods and figure legends are incomplete, posing a barrier to the reproducibility of the study and hindering a comprehensive understanding and accurate interpretation of the results. A critical revision of these aspects is needed, for example:

a. Catalogue numbers of certain products critical to reproduce the study (e.g. antibodies) and/or at what company they have been purchased (e.g. used compounds)

b. On several occasions the used concentrations of drugs or exposure time are not mentioned (e.g. Figure 2H, G (PP2), I, J, K, L, etc.)

c. Figure legend of figure panels E-I in Figure 5 seems to be completely incorrect and not consistent with the figure axis etc.

d. RT-qPCR methodology is not described in Methods.

e. Western blot methods are very limited: these should be described in more detail or cite an article that does.

f. Organoid culture: Information about the source of tumour cells (e.g. pre-treatment biopsy, material after surgery), isolation of tumor cells (e.g. methodology, characterization of material) and culture conditions (e.g. culture time before the experiment) is lacking.

g. Information about how gefitinib/osimertinib-resistant PC9 and HCC827 cells are generated (as well as culture conditions and where they are from) is missing.

We thank the reviewer for pointing these out. We have done our best to add experimental details for reproducibility in methods section and figure legends in lines 343-348, 408-426, 431-432, 439-453, 648-650, 671-672 and 691-693.

(2) Figure 1B/C/D: it would be more meaningful if the most important hits (at least in one of these panels) were highlighted (e.g. line with gene-pair named), or visualized separately, so that the reader does not have to read the supplementary table to know what the most important hits were.

We thank the reviewer for careful concern. We newly added labels for key synergistic gene pairs in figures 1D as reviewer suggested.

(3) qPCR data shown in Figure S4 is from 1 independent experiment. As these experiments (especially qPCR) can be rather variable and the effect size is not very large, I would highly recommend repeating these experiments, or excluding them, as conclusions from them are not solid.

We found performing qPCR with many drugs that did not cause substantial synergistic cell death with NVP-ADW742 in figure S5C (figure S4A in previous version of manuscript) will not provide much additional insights. Also, as we were more interested in finding direct regulators of FYN expression, we focused on drugs that inhibit epigenetic regulator that activate transcription. Therefore, we focused on performing FYN qPCR with drug combinations involving GSK-J4 (KDM6 inhibitor) and pinometostat(DOT1L inhibitor). As shown in our newly added figure in S5D, while GSK-J4 inhibited FYN expression, pinometostat failed to do so. Also, we also confirm that knockout of KDM5 or KDM6 reproducibly failed to decrease FYN expression upon TKI treatment (figure S5E and S5G). The new results are discussed in lines 193-198. We hope these additions satisfy the reviewer.

(4) For validation of synergistic knockouts, it would be helpful for the interpretation to also show the viability/growth of each knockout (or treatment), instead of mostly normalized scores. For example, the reader now has no insight into whether FYN knockout itself already affects cell viability, or not. If it (or EGFR/IGF1R/ABL knockout) would already substantially affect cell viability, a further reduction in cell viability may not be as relevant as when it would not affect cell viability at all.

We thank the reviewer for pointing this out. We replaced our figure in figure 2A to indicate raw changes in cell viability in each single and double knockout cells in figure S2A. We hope this satisfies the reviewer.

(5) The curve fitting as in Figure 2G is somewhat misleading. While the curve seems to be forced to go from 1-0, the +PP2 dose-response curve does actually not seem to start at 1, but rather at 0.8, likely resulting from the effect of PP2 as a single treatment, thus, effects may be interpreted as more synergistic than that they truly are.

The results shown in figure 2G is actually normalized to cells treated or not with PP2 to better reflect the effect of NVP-ADW742, gefitinib and imatinib in the presence of PP2. So viability value starting at 0.8 is not because of the effect of PP2 treatment as single agent (because it is normalized to PP2 treated cells), but is actually because very small dose of particularly NVP-ADW742 resulted in modest decrease in viability. To more accurately depict our findings, we added the data point in figure 2G with TKI dose of 0uM at viability 1. We also added details for normalization of viability in figure legends.

(6) The readability of the paper could be enhanced by higher-quality images (now the text is quite pixelated).

We had technical difficulties in converting file types. We have replaced figures for better resolution for all main and supplementary figures.

(7) The discussion now contains one paragraph about the selectivity of kinase inhibitors, and that repurposing of inhibitors with more relaxed specificity or multi-kinase inhibitors can be beneficial. This does not seem to fall within the scope of the study, as there was no comparison between selective and non-selective inhibitors. It was also not clearly mentioned that the non-selective inhibitors worked better than the gene knockouts, or that for example, KDM3 and KDM4 knockout together worked better than only KDM4 knockout. It is recommended to either remove this paragraph, or rephrase it so that it better fits the actual results

We agree with the reviewer. We chose to remove this paragraph in lines 308-313.

(8) The entire paper does not discuss any known functions of FYN. Its function could be very briefly introduced in the results section when highlighting it as an important hit. More importantly, its known role in cancer and especially drug resistance should be discussed in the discussion (see also Public review).

We thank the reviewer for pointing this out. We added brief description of the role of FYN in cancer malignancy and drug resistance in lines 145-147. Particularly, FYN accumulation by EGR1 transcription factor had been described in the context of imatinib resistant chronic myeloid leukemia (Irwin, Oncotarget, 2015). To address this, we tested whether EGR1 knockout decreases FYN level in MDA-MB-231 (Figure S5A). Notably EGR1 knockout failed to decrease FYN protein level. This result was discussed in lines 187-190.

(9) Textual changes including:

a. Line 29 (and others) "Massively parallel combinatorial CRISPR screens": I would rather choose a more descriptive term, such as "combinatorial tyrosine kinase knockout CRISPR screen", which already clarifies the screen used knockouts of (druggable) tyrosine kinases only. Using both "Parallel" and "combinatorial" is somewhat redundant, and "massively" is subjective, in my opinion.

Manuscript edited as suggested (lines 29, 63, 86, 283). The term “massively parallel” have been removed as they don’t significantly change our scientific findings.

b. Line 67 (and others): "to identify ... for elimination of TNBC": while this may be its potential implication, this study has identified genes in (mostly) TNBC cell lines and cell line xenografts. Please rephrase to something more within the scope of this research.

Manuscript edited as suggested (lines 68-69) as “we utilize CombiGEM-CRISPR technology to identify tyrosine kinase inhibitor combinations with synergistic effect in TNBC cell line and xenograft models for potential combinatorial therapy against TNBC.” We hope it satisfies the reviewer.

c. Line 31 (and others): Please check the capitals of words describing inhibitors, and make them consistent (e.g. Imatinib written with capital I, other inhibitors without capitals).

We thank the reviewer for catching this error. We changed all “imatinib” and “osimertinib” to lowercase.

d. Line 71: "... combining PP2, saracatinib (FYN inhibitor), .." ..." Here it is not clear PP2 is a FYN inhibitor, and, as saracatinib is a well-known Src-inhibitor, it is not correct to just say "FYN inhibitor". Better to rephrase to something such as:  "combining PP2 (Lck/Fyn inhibitor), saracatinib (Src/FYN inhibitor).

As reviewer noted, most Src family kinase inhibitors are not selective against specific member among other Src family members. Therefore, we changed line 73 to “PP2, saracatinib (Src family kinase / FYN inhibitor).”

e. Line 81: "The resulting library enabled massively parallel screens of pairwise knockouts, .." To clarify this is for the selected kinases only: "The resulting library enabled screens of pairwise knockouts of the 76 tyrosine kinase genes, .."

Manuscript edited as suggested by the reviewer in line 86.

f. Line 88 (and others): "after infection" consider rephrasing to "after transduction" as this is more commonly used when using lentiviral vectors only.

We thank the reviewer for this. Every “infection” that designates lentiviral transduction were changed to “transduction”.

g. Line 97-99: While being described as "good" correlation, a correlation of the same sgRNA pair, yet in a different order, of r=0.5 does not seem to be very good, neither does a correlation of r=0.74 for biological replicates. Please consider describing in a less subjective way.

We removed the subjective terms and changed the manuscript as follows: “sgRNA pair (e.g., sgRNA-A + sgRNA-B and sgRNA-B + sgRNA-A) were positively correlated (r = 0.50) and were combined when calculating Z (Fig. S1D). The Z scores for three biological replicates were also correlated with r = 0.74 between replicates #2 and #3 (Fig. S1E).” in lines 97-101.

h. Lines 92-96 and lines 102-115: The results section here contains quite a lot of technical information. While some information may be directly needed to understand the described results (such as a very short and simple explanation of how to interpret gene interaction score), other information may be more appropriate for the Methods section, to enhance the readability of the paper. Consider simplifying here and giving a more detailed overview in the Methods section. Also, the text is not entirely clear. You seem to give two separate explanations of how the GI scores were calculated (Starting in lines 106 and 111): please rephrase and clearly indicate the connections between those two explanations (in the Methods section).

We thank the reviewer for valuable suggestion. We moved significant portions of the technical descriptions in methods section. We also clarified the text regarding the procedures for calculating GI scores in lines 385-387.

i. Line 142: "These findings suggest that gene A could represent an attractive drug target.." "Gene A" should be "FYN"?

We thank the reviewer for catching this. Indeed, it is “FYN” and we changed it in line 154.

j. Line 149: Introduce Saracatinib, and make the reader aware that it actually mostly targets Src, and FYN with lower affinity.

We newly added text in lines 73 and 164 to indicate that saracatinib is an inhibitor against Src family kinases.

k. Line 469: "by the two sgRNA." "by the two sgRNAs".

Corrected

l. Throughout text/figures/figure legends, please check for consistency in the naming of cell lines, compounds, referring to figures etc. (E.g. MDA-MB-231/MDA MB 231/MDAMB-231 ; Fig. 1/Figure 1).

Corrected. Thank you for catching this error.

m. In Methods, frequently ug or uL are used instead of µg or µL

Corrected.

n. Legend Figure 5: Clarify what A, G, I, D, and P mean.

Corrected in line 685-686 to: “A: NVP-ADW742, G: gefitinib, I: imatinib, D: doxorubicin, P: Paclitaxel.”

o. Line 303: What is meant by: "The six variable nucleotides were added in reverse primer for multiplexing". Could you clarify this in the text?

We apologize for confusion the six nucleotides is index sequence for multiplexed run in NGS. The text in lines 373-374 is edited to: “The six nucleotides described as “NNNNNN” in reverse primer above represents unique index to identify biological replicates in multiplexed NGS run.”

Reviewer #2 (Recommendations For The Authors):

To enhance the robustness of the conclusions drawn from this study, certain concerns merit attention.

Concerns:

(1) Line 130 indicates that eight synergistic target gene combinations were validated. It would be helpful to clarify the criteria used to select these gene pairs and provide the rationale for studying these specific combinations of genes.

In fact, we had selected the gene pairs that we had the sgRNAs against available when we performed the experiments, so we did not have very good reason to explain our selections. Instead we added a brief discussion in lines 304-306 that further validations are required for the gene pairs not experimentally tested.

(2) According to Figure 2C, FYN was identified as crucial among the 30 gene pairs, and its upregulation in TNBC prompted further investigation. It would be informative to discuss the expression levels of TEK, FRK, and FGFR2 in TNBC and explain why these nodes were not studied. Is there existing evidence demonstrating the superiority of FYN over these other genes?

The similar concern was raised by reviewer #1. The expression levels of TEK, FRK and FGFR2 were relatively low in MDA-MB-231 and TNBCs in general, and we were concerned about the generalizability of these targets for treating TNBC. While the validation of these genes for possible synthetic lethality may lead to valuable insight, this may be beyond scope of this paper. This concern is newly discussed in result and discussion sections in lines 150-154.

(3) The screening process employed only one cell line, and validation was conducted with only one cell line (Figure 2A). Consider supplementing the findings with more convincing evidence from other breast cancer cell lines to strengthen the conclusions.

Although the CRISPR screens and primary validations were done with only one cell line, further validations with drug combinations were done in independent cancer cell lines such as Hs578T (figures S4E-J). Also, the possible association of FYN expression in drug tolerant cells were also demonstrated in lung cancer cells. We hope this satisfies the reviewer.

(4) The network analysis in Figure 2C lacks a description of the methodology used. It would be beneficial to provide a brief explanation of the methods employed for this analysis.

The network analysis was done manually with the size of each node proportional to the number of gene pairs. We newly added text in figure legend in line 638 to clarify this.

(5) The significance of gene A mentioned in line 142 is unclear. Please provide a clear explanation or context for the importance of this gene.

This is a mistake that were also pointed out by reviewer #1. The “gene A” should have been “FYN”. We corrected this in line 154.

6. In Figure 2J and Figure 2K, it would be more informative to measure the phosphorylation levels of FYN and SRC rather than just their baseline levels. Consider revising the figures accordingly.

We thank the reviewer for a careful comment. We newly provide supplementary figure S5A to show that phosphorylation level of FYN is increased, but this increase was proportional to the increase in FYN protein level, so the ratio of pFYN/FYN did not change significantly. We discussed this result in lines 187-190.

(7) Figure S4B lacks biological replicates, which could impact the reliability of the experimental results. Consider adding biological replicates to enhance the robustness of the findings.

This was also pointed out by reviewer #1. Instead of performing qPCR for all drugs, we focused on validating the decrease in FYN mRNA level for drug combinations that synergistically kill cancer cells. We were also aiming to identify direct mediator of FYN mRNA upregulation, so we focused on drug combination that involves inhibitor of epigenetic regulator that promotes transcription. To this end, we tested the impact of GSK-J4(KDM6 inhibitor) and pinometostat (DOT1L inhibitor) in combination with TKI in regulating FYN expression level. Notably, while GSK-J4 attenuated FYN mRNA accumulation by NVP-ADW742 treatment, pinometostat failed to do so (figure S5C). We newly described these results in lines 192-197 in results section.

(8) Line 186 indicates that KDM3 knockout was not tested in Figure S5A. It would be helpful to provide an explanation for this omission or consider including the data if available.

We thank the reviewer for pointing this out. The T7 endonuclease assay results for KDM3, KDM4 and PHF8 are added in figure S6B. All guide RNAs used in the study efficiently generated indel mutations.

(9) In line 206, KDM4A is introduced, but Figures 3J and 3M had already pointed to KDM4A. The authors did not analyze the ChIP results for other members of the KDM4 family at this point. Please address this inconsistency and provide a rationale for focusing on KDM4A. Additionally, in Figure 3M, consider adding peak labeling to the enriched portion for clarity.

We welcome the reviewer’s careful concern. KDM4 family enzymes perform catalytically identical reactions, and are thought to be redundant. Therefore, we judged that the most abundantly expression genes among KDM4 family should be the primary target to focus on. To this end, we analyzed the expression levels of KDM4 family genes in supplementary figure S6A. Indeed KDM4A expression was the highest among other KDM4 family genes. We discussed this in results section in lines 218-220.

(10) The author only indicated the relationship between the H3K9me3 level in the enhancer region and FYN expression. It would be valuable to verify the activity of the enhancers and investigate additional markers such as H3K27ac and H3K4me1. Consider discussing these aspects to provide a more comprehensive understanding.

Since we and others had shown that histone dementhylases are increased upon drug treatment, we focused on histone methylation marks which are associated with gene repression and whose removal by demethylases are associated with drug resistance. To this end, KDM6 demethylases removing H3K27me3 may serve as attractive alternative. In our newly added supplementary figure S6E, ADW742 treatment did not decrease H3K27me3 level in FYN promoter, indicating that H3K9me3 may be the dominant epigenetic change that modulates FYN expression upon drug treatment. This was briefly discussed in lines 233-235.

(11) In Figure 4A, the addition of the drug alone does not inhibit tumor growth. Please provide an explanation for this result and consider discussing potential reasons for the observed lack of inhibition.

The drug dose was adjusted carefully to minimize tumor shrinkage by single drug so that synergistic tumor shrinkage can be clearer.

(12) Line 208 indicates missing parentheses in the text describing Figure 4C. Please correct the text accordingly to ensure clarity.

Corrected. Thank you for catching this error.

(13) The figure legends for Figures 5E, F, G, and H contain errors. Please correct the figure legends to accurately describe the respective figures.

We thank the reviewer for catching this error. We have changed the figure legends in lines 691-697 to accurately describe the figures.

(14) It may be beneficial for the authors to divide the results section into several subsections and add headings to improve the overall understanding of the findings.

This is an excellent suggestion. We divided our results section into subsections and added headings in lines 80, 141, 181, 237 and 251 to help readers understand our findings.

(15) The authors should include the sgRNA sequences used for gene targeting, along with details of the target genes and negative/positive controls, in the Supplementary Materials to enhance reproducibility and transparency.

This is a critical point for improving reproducibility of our work. The sgRNA sequences used in the study are newly added in supplementary table S3.

(16) The resolution of the figures in the Supplementary Materials is too low, which may impede the authors' ability to interpret the data. Consider providing higher-resolution figures for better readability.

We had similar concern posed by reviewer #1, we provided higher resolution image for all main and supplementary figures.

Author response:

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

Reviewer #1 (Public Review):

Summary:

The authors constructed a novel HSV-based therapeutic vaccine to cure SIV in a primate model. The novel HSV vector is deleted for ICP34.5. Evidence is given that this protein blocks HIV reactivation by interference with the NF-kB pathway. The deleted construct supposedly would reactivate SIV from latency. The SIV genes carried by the vector ought to elicit a strong immune response. Together the HSV vector would elicit a shock and kill effect. This is tested in a primate model.

Thank you for your kind comments and suggestions, which are very helpful in improving our manuscript. We have carefully revised our manuscript and performed additional experiments accordingly, and we now think this version has been substantially improved for your reconsideration.

Strengths and weaknesses:

(1) Deleting ICP34.5 from the HSV construct has a very strong effect on HIV reactivation. Why is no eGFP readout given in Figure 1C as for WT HSV? The mechanism underlying increased activation by deleting ICP34.5 is only partially explored. Overexpression of ICP34.5 has a much smaller effect (reduction in reactivation) than deletion of ICP34.5 (strong activation); so the story seems incomplete.

Thank you for your careful review and kind reminder.

(1) We are sorry for the misunderstanding of Figure 1C. In the experiment of Figue 1C, we used an HSV-1 17 strain containing GFP (HSV-GFP) and HSV-DICP34.5 (recombinant HSV-1 17 strain with ICP34.5 deletion based on HSV-GFP) to reactivate the HIV latency cell line (J-Lat 10.6 cell). Since detecting GFP cannot distinguish between HSV infection and HIV reactivation, we assessed the reactivation by measuring the mRNA levels of HIV LTR upon stimulation with either HSV-GFP or HSV-ΔICP34.5. Actually, in Figure 1B, we had verified the reactivation efficacy by infecting J-Lat 10.6 cells with the HSV-1 17 strain containing GFP (HSV-GFP) and found significant upregulation of mRNA levels of HIV-1 LTR, Tat, Gag, Vif, and Vpr. We have adjusted the corresponding descriptions accordingly in the revised manuscript.

(2) We agree with your insightful mention that the mechanism underlying increased activation by HSV-ΔICP34.5 is worthy to be further explored in the future study. In this study, we found that ICP34.5 play an antagonistic role with the reactivation of HIV latency by HSV-1 mainly through the modulation of host NF-κB and HSF1 pathways, while HSV-1 (especially HSV-ΔICP34.5) might reactivate HIV latency through NF-κB, HSF1, and other yet-to-be-determined mechanisms. Thus, ICP34.5 overexpression can only a partial effect on the reduction of the HIV latency reactivation by HSV-1. We have mentioned this issue in the revised “Discussion section”. “Intriguingly, these findings collectively indicated that ICP34.5 might play an antagonistic role in the reactivation of HIV by HSV-1, and thus our modified HSV-DICP34.5 constructs can effectively reactivate HIV/SIV latency through the release of imprisonment from ICP34.5. However, ICP34.5 overexpression had only a partial effect on the reduction of the HIV latency reactivation, indicating that HSV-DICP34.5-based constructs can also reactivate HIV latency through other yet-to-be-determined mechanisms.” (Lines 334 to 340).

(2) No toxicity data are given for deleting ICP34.5. How specific is the effect for HIV reactivation? An RNA seq analysis is required to show the effect on cellular genes.

Thank you for your questions and suggestions.

(1) It’s well known that ICP34.5 is a neurotoxicity factor that can antagonize host immune responses, and previous studies (in gene therapy and oncolytic virotherapy) have shown that the safety of recombinant HSV-based vector can be improved by deleting ICP34.5. In this study, we also found that HSV-DICP34.5 exhibited lower virulence and replication ability than its parental strain (HSV-GFP) (Figure 1D, Figure S1). In addition, HSV-DICP34.5 induced a lower level of inflammatory cytokines (including IL-6, IL-1β, and TNF-α) in primary CD4+ T cells from PLWH compared to HSV-GFP stimulation, likely due to its lower virulence and replication ability (Figure 1I-K). In addition, the CD4+ /CD8+ T cell ratio (Figure 5I) and body weight (Figure S9) after treatment were effectively ameliorated in the SIV-infected macaques of the ART+HSV-DICP34.5-sPD1-SIVgag/SIVenv group. Our data also demonstrated that there was no significant effect on the cell composition of peripheral blood in the SIV-infected macaques of ART+HSV-sPD1-SIVgag/SIVenv group (Figure S10). Thus, these data suggest the safety of HSV-DICP34.5 in PLWH might be tolerable. We have added the corresponding description in the revised manuscript.

(2) In our study, we found both adenovirus and vaccinia virus cannot reactivate HIV latency (Figure S3). In addition, the deletion of ICP0 gene from HSV-1 diminished the reactivation effect of HIV latency by HSV-1 (Figure S4). Thus, these data suggested the reactivation of HIV latency by HSV-1 might be virus-specific. Of course, this might be further investigated in future studies. We have added the corresponding description in the revised manuscript.

(3) To explore the mechanism of reactivating viral latency by HSV-DICP34.5-based constructs, we performed RNA-seq analysis (Figure S5). We have added the corresponding description accordingly in the revised manuscript.

(3) The primate groups are too small and the results to variable to make averages. In Figure 5, the group with ART and saline has two slow rebounders. It is not correct to average those with a single quick rebounder. Here the interpretation is NOT supported by the data.

We agree with you that this is a pilot study with limited numbers of rhesus macaques. Although the number of macaques was relatively limited, these nine macaques were distributed evenly based on the background level of age, sex, weight, CD4 count, and viral load (VL) (Table S2). All SIV-infected macaques used in this study had a long history of SIV infection and had several courses of ART therapy, which mimics treatment of chronic HIV-1 infection in humans. These macaques were infected with SIVmac239 for more than 5 years, and highly pathogenic SIV-infected macaques have been well-validated as a stringent model to recapitulate HIV-1 pathogenesis and persistence during ART therapy in humans. Indeed, in our Chinese rhesus model, ART treatment effectively suppressed SIV infection to undetectable levels in plasma, and upon ART discontinuation, virus rapidly rebounded, which is very similar with that in ART-treated HIV patients. We think the results of this pilot study were very promising for further studies which will be expanded the scale of animals and then to preclinical and clinical study in our next projects. Thank you for your understanding.

As for your question regarding “the two animals with low VL and slow rebound”, our explanation is following: As mentioned above, these macaques were distributed evenly based on the background level of CD4 count and VL (Table S2), and then there were different change of viral load and viral rebound in different groups. Thus, we think these data can support our interpretation. Moreover, our conclusion can also be supported from at least three evidences.

(1) The VL in the ART+saline group promptly rebounded after ART discontinuation, with an average 8.63-fold increase in the rebounded peak VL compared with the pre-ART VL (Figure 5A, D and E). However, plasma VL in the ART+HSV-sPD1-SIVgag/SIVenv group exhibited a delayed rebound interval (Figure 5B-D).

(2) There was a lower rebounded peak VL than pre-ART VL in the ART+HSV-sPD1-SIVgag/SIVenv group (average 12.20-fold decrease), while a higher rebounded peak VL than pre-ART VL in the ART+HSV-empty group (average 2.74-fold increase) (Figure 5E).

(3） We found significant suppression of total SIV DNA and integrated SIV DNA provirus in the ART+HSV-sPD1-SIVgag/SIVenv group. However, the copies of the SIV DNA provirus were significantly improved in the ART+HSV-empty group and ART+saline group (Figure 5F-G).

Thank you for your understanding.

Discussion

HSV vectors are mainly used in cancer treatment partially due to induced inflammation. Whether these are suitable to cure PLWH without major symptoms is a bit questionable to me and should at least be argued for.

Thank you for your kind question comment and question. We confirmed the enhanced reactivation of HIV latency by HSV-∆ICP34.5 in primary CD4+ T cells from people living with HIV (PLWH) (Figure S2). As mentioned above, previous studies have shown that the safety of recombinant HSV-based vector can be improved by deleting ICP34.5. In this study, we also found that HSV-DICP34.5 exhibited lower virulence and replication ability than its parental strain (HSV-GFP) (Figure 1D, Figure S1). In addition, HSV-DICP34.5 induced a lower level of inflammatory cytokines (including IL-6, IL-1β, and TNF-α) in primary CD4+ T cells from PLWH compared to HSV-GFP stimulation, likely due to its lower virulence and replication ability (Figure 1I-K). In addition, the CD4+ /CD8+ T cell ratio (Figure 5I) and body weight (Figure S9) after treatment were effectively ameliorated in the SIV-infected macaques of the ART+HSV-DICP34.5-sPD1-SIVgag/SIVenv group. Our data also demonstrated that there was no significant effect on the cell composition of peripheral blood in the SIV-infected macaques of ART+HSV-sPD1-SIVgag/SIVenv group (Figure S10). Thus, these data suggest the safety of HSV-DICP34.5 in PLWH might be tolerable. We have added the corresponding description in the revised manuscript.

Reviewer #2 (Public Review):

Summary:

In this article, Wen et. al. describe the development of a 'proof-of-concept' bi-functional vector based on HSV-deltaICP-34.5's ability to purge latent HIV-1 and SIV genomes from cells. They show that co-infection of latent J-lat T-cell lines with an HSV-deltaICP-34.5 vector can reactivate HIV-1 from a latent state. Over- or stable expression of ICP 34.5 ORF in these cells can arrest latent HIV-1 genomes from transcription, even in the presence of latency reversal agents. ICP34.5 can co-IP with- and de-phosphorylate IKKa/b to block its interaction with NF-k/B transcription factor. Additionally, ICP34.5 can interact with HSF1 which was identified by mass-spec. Thus, the authors propose that the latency reversal effect of HSV-deltaICP-34.5 in co-infected JLat cells is due to modulatory effects on the IKKa/b-NF-kB and PP1-HSF-1 pathway.

Next, the authors cleverly construct a bifunctional HSV-based vector with deleted ICP34.5 and 47 ORFs to purge latency and avoid immunological refluxes, and additionally, expand the application of this construct as a vaccine by introducing SIV genes. They use this 'vaccine' in mouse models and show the expected SIV-immune responses. Experiments in rhesus macaques (RM), further elicit the potential for their approach to reactivate SIV genomes and at the same time block their replication by antibodies. What was interesting in the SIV experiments is that the dual-functional vector vaccine containing sPD1- and SIV Gag/Env ORFs effectively delayed SIV rebound in RMs and in some cases almost neutralized viral DNA copy detection in serum. Very promising indeed, however, there are some questions I wish the authors had explored to get answers to, detailed below.

Overall, this is an elegant and timely work demonstrating the feasibility of reducing virus rebound in animals, with the potential to expand to clinical studies. The work was well-written, and sections were clearly discussed.

Strengths:

The work is well designed, rationale explained, and written very clearly for lay readers.<br /> Claims are adequately supported by evidence and well-designed experiments including controls.

Thank you for your nice comments regarding our work.

Weaknesses:

(1) While the mechanism of ICP34.5 interaction and modulation of the NF-kB and HSF1 pathways are shown, this only proves ICP34.5 interactions but does not give away the mechanism of how the HSV-deltaICP-34.5 vector purges HIV-1 latency. What other components of the vector are required for latency reversal? Perhaps serial deletion experiments of the other ORFs in the HSV-deltaICP-34.5 vector might be revealing.

Thank you for your valuable suggestion. In fact, we are currently further exploring some potential viral genes of HSV-1 that might play a role in the reactivation of HIV latency. We have found that the deletion of ICP0 gene from HSV-1 diminished the reactivation effect of HIV latency by HSV-1 (Figure S4), showing that ICP0 might play a vital role for the reactivation. Of course, this might be further investigated in future studies. We have added the corresponding description in the revised manuscript.

(2) The efficacy of the HSV vaccine vectors was evaluated in Rhesus Macaque model animals. Animals were chronically infected with SIV (a parent of HIV), treated with ART, challenged with bi-functional HSV vaccine or controls, and discontinued treatment, and the resulting virus burden and immune responses were monitored. The animals showed SIV Gag and Env-specific immune responses, and delayed virus rebound (however rebound is still there), and below-detection viral DNA copies. What would make a more convincing argument to this reviewer will be data to demonstrate that after the bi-functional vaccine, the animals show overall reduction in the number of circulating latent cells. The feasibility of obtaining such a result is not clearly demonstrated.

Thank you for your valuable mention. We have now provided more data about this issue. We found significant suppression of total SIV DNA and integrated SIV DNA provirus in the ART+HSV-sPD1-SIVgag/SIVenv group. However, the copies of the SIV DNA provirus were significantly improved in the ART+HSV-empty group and ART+saline group (Figure 5F-G). We have added the corresponding description in the revised manuscript.

(3) The authors state that the reduced virus rebound detected following bi-functional vaccine delivery is due to latent genomes becoming activated and steady-state neutralization of these viruses by antibody response. This needs to be demonstrated. Perhaps cell-culture experiments from specimens taken from animals might help address this issue. In lab cultures one could create environments without antibody responses, under these conditions one would expect a higher level of viral loads to be released in response to the vaccine in question.

Thanks for your kind mention and suggestion. We performed the following cell experiment to address this issue. Primary CD4+ T cells from people living with HIV (PLWH) were isolated, and then infected with HSV or HSV-∆ICP34.5 constructs. As expected, we confirmed the enhanced reactivation of HIV latency by HSV-∆ICP34.5 (Figure S2). Thank you.

(4) How do the authors imagine neutralizing HIV-1 envelope epitopes by a similar strategy? A discussion of this point may also help.

Thank you for your kind comment. We have added the corresponding discussion in the revised manuscript. “The current consensus on HIV/AIDS vaccines emphasizes the importance of simultaneously inducing broadly neutralizing antibodies and cellular immune responses. Therefore, we believe that incorporating the induction of broadly neutralizing antibodies into our future optimizing approaches may lead to better therapeutic outcomes.” (Lines 384 to 388)

(5) I thought the empty HSV-vector control also elicited somewhat delayed kinetics in virus rebound and neutralization, can the authors comment on why this is the case?

Thank you for your careful review and mention. We agree with you that the HSV-1 empty vector does exhibit somewhat a delayed rebound. We think the possible reason is: Although the empty HSV-vector cannot elicit SIV-specific CTL responses, it effectively activates the latent SIV reserviors, and then these activated virions can be partially killed by ART drugs. Therefore, even without carrying HIV/SIV antigens, somewhat delayed kinetics in virus rebound may be observed. Thank you.

Reviewer #1 (Recommendations For The Authors):

(1) The authors should provide toxicity data for HSV transduction after deleting ICP34.5 and provide an explanation of why overexpression of ICP34.5 has such a small effect.

Thank you for your questions and suggestions. As mentioned above, we now provided data for the safety of HSV-DICP34.5-based constructs.

(1) It’s well known that ICP34.5 is a neurotoxicity factor that can antagonize host immune responses, and previous studies (in gene therapy and oncolytic virotherapy) have shown that the safety of recombinant HSV-based vector can be improved by deleting ICP34.5. In this study, we also found that HSV-DICP34.5 exhibited lower virulence and replication ability than its parental strain (HSV-GFP) (Figure 1D, Figure S1). In addition, HSV-DICP34.5 induced a lower level of inflammatory cytokines (including IL-6, IL-1β, and TNF-α) in primary CD4+ T cells from PLWH compared to HSV-GFP stimulation, likely due to its lower virulence and replication ability (Figure 1I-K). In addition, the CD4+ /CD8+ T cell ratio (Figure 5I) and body weight (Figure S9) after treatment were effectively ameliorated in the SIV-infected macaques of the ART+HSV-DICP34.5-sPD1-SIVgag/SIVenv group. Our data also demonstrated that there was no significant effect on the cell composition of peripheral blood in the SIV-infected macaques of ART+HSV-sPD1-SIVgag/SIVenv group (Figure S10). Thus, these data suggest the safety of HSV-DICP34.5 in PLWH might be tolerable. We have added the corresponding description in the revised manuscript.

(2) We agree with your insightful mention that the mechanism underlying increased activation by HSV-ΔICP34.5 is worthy to be further explored in the future study. In this study, we found that ICP34.5 play an antagonistic role with the reactivation of HIV latency by HSV-1 mainly through the modulation of host NF-κB and HSF1 pathways, while HSV-1 (especially HSV-ΔICP34.5) might reactivate HIV latency through NF-κB, HSF1, and other yet-to-be-determined mechanisms. Thus, ICP34.5 overexpression can only a partial effect on the reduction of the HIV latency reactivation by HSV-1. We have mentioned this issue in the revised “Discussion section”. “Intriguingly, these findings collectively indicated that ICP34.5 might play an antagonistic role in the reactivation of HIV by HSV-1, and thus our modified HSV-DICP34.5 constructs can effectively reactivate HIV/SIV latency through the release of imprisonment from ICP34.5. However, ICP34.5 overexpression had only a partial effect on the reduction of the HIV latency reactivation, indicating that HSV-DICP34.5-based constructs can also reactivate HIV latency through other yet-to-be-determined mechanisms.” (Lines 334 to 340).

(2) How specific is the effect for HIV reactivation? An RNA seq analysis is required to show the effect on cellular genes.

Thank you for your questions and suggestions.

(1) In our study, we found both adenovirus and vaccinia virus cannot reactivate HIV latency (Figure S3). In addition, the deletion of ICP0 gene from HSV-1 diminished the reactivation effect of HIV latency by HSV-1 (Figure S4). Thus, these data suggested the reactivation of HIV latency by HSV-1 might be virus-specific. Of course, this might be further investigated in future studies. We have added the corresponding description in the revised manuscript.

(2) To explore the mechanism of reactivating viral latency by HSV-DICP34.5-based constructs, we performed RNA-seq analysis (Figure S5). Results showed that there were numerous differentially expressed genes (DEGs) in response to HSV-ΔICP34.5 infection. Among them, 2288 genes were upregulated, and 611 genes were downregulated. GO analysis showed the enrichment of these DEGs in cellular cycle, cellular development, and cellular proliferation, and KEGG enrichment analysis indicated the enrichment in pathways such as cellular cycle and cytokine-cytokine receptor interaction. We have added the corresponding description accordingly in the revised manuscript.

(3) A comparison in primates has to be given for constructs with or without ICP34.5 to validate cell culture data (what is an empty vector?)

Thank you for your reminder. In the revised manuscript, we performed the following cell experiment to address this issue. Primary CD4+ T cells from people living with HIV (PLWH) were isolated, and then infected with HSV or HSV-∆ICP34.5 constructs. As expected, we confirmed the enhanced reactivation of HIV latency by HSV-∆ICP34.5 (Figure S2). Thank you.

(4) Legends should be improved in writing and content.

Thank you for your kind mention. In the revised version, we have improved both the manuscript content and the legends of all Figures have been carefully revised in writing and content. Thank you.

(5) The primate groups should be enlarged before any reliable conclusions can be made. Inflammatory/tox data should be provided.

Thank you for your question.

(1) As mentioned above, we agree with you that this is a pilot study with limited numbers of rhesus macaques. Although the number of macaques was relatively limited, these nine macaques were distributed evenly based on the background level of age, sex, weight, CD4 count, and viral load (VL) (Table S2). All SIV-infected macaques used in this study had a long history of SIV infection and had several courses of ART therapy, which mimics treatment of chronic HIV-1 infection in humans. These macaques were infected with SIVmac239 for more than 5 years, and highly pathogenic SIV-infected macaques have been well-validated as a stringent model to recapitulate HIV-1 pathogenesis and persistence during ART therapy in humans. Indeed, in our Chinese rhesus model, ART treatment effectively suppressed SIV infection to undetectable levels in plasma, and upon ART discontinuation, virus rapidly rebounded, which is very similar with that in ART-treated HIV patients. We think the results of this pilot study were very promising for further studies which will be expanded the scale of animals and then to preclinical and clinical study in our next projects. Thank you for your understanding.

(2) As well known, ICP34.5 is a neurotoxicity factor that can antagonize host immune responses, and previous studies have shown that the safety of recombinant HSV-based vector can be improved by deleting ICP34.5. In this study, we also found that HSV-DICP34.5 exhibited lower virulence and replication ability than its parental strain (HSV-GFP) (Figure 1D, Figure S1). In addition, HSV-DICP34.5 induced a lower level of inflammatory cytokines (including IL-6, IL-1β, and TNF-α) in primary CD4+ T cells from PLWH compared to HSV-GFP stimulation, likely due to its lower virulence and replication ability (Figure 1I-K). In addition, the CD4+ /CD8+ T cell ratio (Figure 5I) and body weight (Figure S9) after treatment were effectively ameliorated in the SIV-infected macaques of the ART+HSV-DICP34.5-sPD1-SIVgag/SIVenv group. Our data also demonstrated that there was no significant effect on the cell composition of peripheral blood in the SIV-infected macaques of ART+HSV-sPD1-SIVgag/SIVenv group (Figure S10). Thus, these data suggest the safety of HSV-DICP34.5 in PLWH might be tolerable. We have added the corresponding description in the revised manuscript.

(6) Discuss the potential of inflammatory HSV vaccines to be used in PLWH without clinical symptoms.

Thank you for your mention. As discussed above, we found that HSV-DICP34.5 exhibited lower virulence and replication ability than its parental strain (Figure 1D, Figure S1), and we also found that HSV-DICP34.5 induced a lower level of inflammatory cytokines (including IL-6, IL-1β, and TNF-α) in primary CD4+ T cells from PLWH compared to HSV-GFP stimulation, likely due to its lower virulence and replication ability (Figure 1I-K). In addition, the CD4+ /CD8+ T cell ratio (Figure 5I) and body weight (Figure S9) after treatment were effectively ameliorated in the SIV-infected macaques of the ART+HSV-DICP34.5-sPD1-SIVgag/SIVenv group. Our data also demonstrated that there was no significant effect on the cell composition of peripheral blood in the SIV-infected macaques of ART+HSV-sPD1-SIVgag/SIVenv group (Figure S10). Thus, these data suggest the safety of HSV-DICP34.5 in PLWH might be tolerable. We have added the corresponding description in the revised manuscript.

Reviewer #2 (Recommendations For The Authors):

I think the authors have done due diligence to the experimental system, and collected evidence to show the feasibility of delaying virus rebound in macaques. However, I would encourage the authors to perform experiments that can back up the claim that delayed virus rebound is due to neutralization effects, or perhaps due to a reduction in viral reservoir. I believe insights into this process will add rigor, and push the relevance of the study to the next level.

Thank you for your nice comment and valuable suggestion. We have now provided more data about this issue. We found significant suppression of total SIV DNA and integrated SIV DNA provirus in the ART+HSV-sPD1-SIVgag/SIVenv group. However, the copies of the SIV DNA provirus were significantly improved in the ART+HSV-empty group and ART+saline group (Figure 5F-G). We also discussed that incorporating the induction of broadly neutralizing antibodies into our future optimizing approaches may lead to better therapeutic outcomes in the revised Discussion section. We have added the corresponding description in the revised manuscript. Thank you.

Altogether, all of the above comments and suggestions are very helpful in improving our manuscript. We have taken these comments into account seriously and try our best to address these questions point-by-point. After making extensive revisions, we now submit this revised manuscript for your re-consideration. Thank you again for all of your comments and suggestions.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This study uses single nucleus multiomics to profile the transcriptome and chromatin accessibility of mouse XX and XY primordial germ cells (PGCs) at three time-points spanning PGC sexual differentiation and entry of XX PGCs into meiosis (embryonic days 11.5-13.5). They find that PGCs can be clustered into sub-populations at each time point, with higher heterogeneity among XX PGCs and more switch-like developmental transitions evident in XY PGCs. In addition, they identify several transcription factors that appear to regulate sex-specific pathways as well as cell-cell communication pathways that may be involved in regulating XX vs XY PGC fate transitions. The findings are important and overall rigorous. The study could be further improved by a better connection to the biological system, including the addition of experiments to validate the 'omics-based findings in vivo and putting the transcriptional heterogeneity of XX PGCs in the context of findings that meiotic entry is spatially asynchronous in the fetal ovary. Overall, this study represents an advance in germ cell regulatory biology and will be a highly used resource in the field of germ cell development.

Strengths:

(1) The multiomics data is mostly rigorously collected and carefully interpreted.

(2) The dataset is extremely valuable and helps to answer many long-standing questions in the field.

(3) In general, the conclusions are well anchored in the biology of the germ line in mammals.

Weaknesses:

(1) The nature of replicates in the data and how they are used in the analysis are not clearly presented in the main text or methods. To interpret the results, it is important to know how replicates were designed and how they were used. Two "technical" replicates are cited but it is not clear what this means.

The two independent technical replicates comprised different pools of paired gonads. This sentence was added to the methods section of the revised manuscript.

(2) Transcriptional heterogeneity among XX PGCs is mentioned several times (e.g., lines 321-323) and is a major conclusion of the paper. It has been known for a long time that XX PGCs initiate meiosis in an anterior-to-posterior wave in the fetal ovary starting around E13.5. Some heterogeneity in the XX PGC populations could be explained by spatial position in the ovary without having to invoke novel subpopulations.

We thank the reviewer for pointing out this important biological phenomenon. We also recognize that transcriptional heterogeneity among XX PGCs is likely due to the anterior-to-posterior wave of meiotic initiation in E13.5 ovaries and highlight this possibility in our manuscript. However, since our study utilizes single-nucleus RNA-sequencing and not spatial transcriptomics, we are not able to capture the spatial location of the XX PGCs analyzed in our dataset. As such, our analysis applied clustering tools to classify the populations of XX PGCs captured in our dataset. 

(3) There is essentially no validation of any of the conclusions. Heterogeneity in the expression of a given marker could be assessed by immunofluorescence or RNAscope.

In our revised manuscript, we included immunofluorescence staining of potential candidate factors involved in PGC sex determination, such as PORCN and TFAP2C. Testing and optimizing antibodies for the targets identified in this study are ongoing efforts in our lab and we look forward to sharing our results with the research community.

(4) The paper sometimes suffers from a problem common to large resource papers, which is that the discussion of specific genes or pathways seems incomplete. An example here is from the analysis of the regulation of the Bnc2 locus, which seems superficial. Relatedly, although many genes and pathways are nominated for important PGC functions, there is no strong major conclusion from the paper overall.

In this manuscript, we set out to identify candidate factors, some already known and many others unknown, involved in the developmental pathways of PGC sex determination using computational tools. Our goal, as a research group and with future collaborators, is to screen these interesting candidates and discover their function in the primordial germ cell. Our research, presented in this study, represents a launching pad for which to identify future projects that will investigate these factors in further detail.

Reviewer #2 (Public Review):

Summary:

This manuscript by Alexander et al describes a careful and rigorous application of multiomics to mouse primordial germ cells (PGCs) and their surrounding gonadal cells during the period of sex differentiation.

Strengths:

In thoughtfully designed figures, the authors identify both known and new candidate gene regulatory networks in differentiating XX and XY PGCs and sex-specific interactions of PGCs with supporting cells. In XY germ cells, novel findings include the predicted set of TFs regulating Bnc2, which is known to promote mitotic arrest, as well as the TFs POU6F1/2 and FOXK2 and their predicted targets that function in mitosis and signal transduction. In XX germ cells, the authors deconstruct the regulation of the premeiotic replication regulator Stra8, which reveals TFs involved in meiosis, retinoic acid signaling, pluripotency, and epigenetics among predictions; this finding, along with evidence supporting the regulatory potential of retinoic acid receptors in meiotic gene expression is an important addition to the debate over the necessity of retinoic acid in XX meiotic initiation. In addition, a self-regulatory network of other TFs is hypothesized in XX differentiating PGCs, including TFAP2c, TCF5, ZFX, MGA, and NR6A1, which is predicted to turn on meiotic and Wnt signaling targets. Finally, analysis of PGC-support cell interactions during sex differentiation reveals more interactions in XX, via WNTs and BMPs, as well as some new signaling pathways that predominate in XY PGCs including ephrins, CADM1, Desert Hedgehog, and matrix metalloproteases. This dataset will be an excellent resource for the community, motivating functional studies and serving as a discovery platform.

Weaknesses:

My one major concern is that the conclusion that PGC sex differentiation (as read out by transcription) involves chromatin priming is overstated. The evidence presented in the figures includes a select handful of genes including Porcn, Rimbp1, Stra8, and Bnc2 for which chromatin accessibility precedes expression. Given that the authors performed all of their comparisons between XX versus XY datasets at each timepoint, have they missed an important comparison that would be a more direct test of chromatin priming: between timepoints for each sex? Furthermore, it remains possible that common mechanisms of differentiation to XX and XY could be missing from this analysis that focused on sexspecific differences.

We thank the reviewer for their thoughtful assessment and suggestions, as stated here. We note that chromatin priming in PGCs prior to sex determination is a well-documented research finding (see references below), that is further supported by our single-nucleus multiomics data. To support these findings previously stated in the scientific literature, we included data demonstrating the asynchronous correlation between chromatin accessibility and gene expression during PGC sex determination. Specifically, we investigated the associations of differentially accessible chromatin peaks with differentially expressed gene expression for each PGC type (between sexes and across embryonic stages) using computational tools and methods that are well-established and applied by the research community. In our manuscript, we note that the patterns we identified support the potential role of chromatin priming in PGC sex determination. Nevertheless, we further highlight that a comprehensive profile of 3D chromatin structure and enhancer-promoter contacts in differentiating PGCs is needed to fully understand how changes to chromatin facilitate PGC sex determination.

References:

(1) Chen, M., et al. Integration of single-cell transcriptome and chromatin accessibility of early gonads development among goats, pigs, macaques, and humans. Cell Reports 41 (2022).

(2) Huang, T.-C. et al. Sex-specific chromatin remodelling safeguards transcription in germ cells. Nature 600, 737–742 (2021).

Reviewer #3 (Public Review):

Summary:

Alexander et al. reported the gene-regulatory networks underpinning sex determination of murine primordial germ cells (PGCs) through single-nucleus multiomics, offering a detailed chromatin accessibility and gene expression map across three embryonic stages in both male (XY) and female (XX) mice. It highlights how regulatory element accessibility may precede gene expression, pointing to chromatin accessibility as a primer for lineage commitment before differentiation. Sexual dimorphism in these elements and gene expression increases over time, and the study maps transcription factors regulating sexually dimorphic genes in PGCs, identifying sex-specific enrichment in various transcription factors. Strengths:

The study includes step-wise multiomic analysis with some computational approach to identify candidate TFs regulating XX and XY PGC gene expression, providing a detailed timeline of chromatin accessibility and gene expression during PGC development, which identifies previously unknown PGC subpopulations and offers a multimodal reference atlas of differentiating PGC clusters. Furthermore, the study maps a complex network of transcription factors associated with sex determination in PGCs, adding depth to our understanding of these processes.

Weaknesses:

While the multiomics approach is powerful, it primarily offers correlational insights between chromatin accessibility, gene expression, and transcription factor activity, without direct functional validation of identified regulatory networks.

As stated in our response above to a similar concern, we note that our research study represents a launching pad for which to identify future projects that will investigate candidates that may be involved in PGC sex determination, in further detail. With this rich dataset in hand, our goal in future research projects is to screen these candidates and discover their function in PGCs. 

Response to Recommendations

Reviewer #1 (Recommendations For The Authors):

(1) Clarify at first introduction how combined ATAC-seq/RNA-seq mulitomics libraries were prepared, including if ATAC and RNA-seq data are from the same cell.

This information was added to the introduction of the revised manuscript.

(2) Clarify what the two technical replicates represent. Are they two libraries from the same gonad or the same pool of gonads? Are they from 2 different gonads?

The two independent technical replicates comprised different pools of paired gonads. This sentence was added to the methods section of the revised manuscript.

(3) In Supplemental Figure 1, there is substantial variation in the number of unique snATAC-seq fragments between some conditions. Could this create a systematic bias that affects clustering?

We recognize the concern that substantial variation in the number of unique snATAC-seq fragments between conditions could potentially create a systematic bias that affects clustering. However, we analyzed our snATAC-seq dataset with Signac, which performs term frequency-inverse document frequency (TF-IDF) normalization. This is a process that normalizes across cells to correct for differences in cellular sequencing depth. Given that sequencing depth was taken into account in our normalization and clustering procedures, and that the unbiased clustering of PGCs also reflects the sex and embryonic stage of PGCs, we are confident that the clustering of the snATAC-seq datasets closely reflects the biological variability present in the PGCs collected.

References:

Signac Website:  https://stuartlab.org/signac/articles/pbmc_vignette

Stuart, T., Srivastava, A., Madad, S., Lareau, C. A., & Satija, R. (2021). Single-cell chromatin state analysis with Signac. Nature methods, 18(11), 1333-1341.

(4) In Figures 2a, 2e, 3a, and 3e, the visualization scheme is very difficult to follow. It's very hard to see the colors corresponding to average expression for many genes because the circles are so small. In addition, the yellow color is hard to see and makes it hard to estimate the size of the circle since the boundaries can be indistinct. I recommend using a different visualization scheme and/or set of size scales be used.

In Figures 2a, 2e, 3a, and 3e, we chose this color palette to be inclusive of viewers who are colorblind. The chosen colors are visible on both a computer screen and on printed paper. We also included a legend of the color scale and dot size representing the average expression and percent of cells expressing the gene, respectively. If the color cannot be seen, it is because the cell population is not expressing the gene.

(5) Perform in vivo validation (immunofluorescence or RNAscope) of at least some targets implicated in PGC development by this study.

Such validations (immunofluorescence staining of PORCN and TFAP2C) are now included in Figure 4 and the supplement.

(6) In line 351, the authors state that "we observed a strong demarcation between XX and XY PGCs at E12.5-E13.5." But in Figure 1j it looks like a reasonably high fraction of both XX and XY E12.5 cells are in cluster 1, which should mean that there is some overlap.

While it is true that Figure 1j shows overlap of both XX and XY E12.5 cells in cluster 1, we were commenting on the separation of E12.5 XX (clusters 4 and 5) and E12.5 XY (clusters 8 and 9) PGCs. We have modified the sentence beginning at line 351 to state that the separation between XX and XY PGCs occurs at E13.5.

(7) In lines 404-405: "We first linked snATAC-seq peaks to XY PGC functional genes". It is important to know how the peaks were linked to genes.

We added the following sentence to address this comment: “Peak-to-gene linkages were determined using Signac functionalities and were derived from the correlation between peak accessibility and the intensity of gene expression.”

(8) In Supplemental Figure 5c, the XX E11.5 condition has a substantially higher fraction of ATAC peaks at promoter regions compared to the others. Does this have statistical and biological significance?

This is an interesting observation beyond the scope of our manuscript. Many interesting questions arise from this study and it is our plan to investigate further in the future. 

(9) Line 885: "The increased number of DA peaks at E13.5 may be the result of changes to chromatin structure as XX PGCs enter meiotic prophase I"; but in Figure 4b, there's only a modest increase in DAP number from E12.5 to E13.5 in XX PGCs, compared to a massive gain in XY PGCs.

In our manuscript, we comment on both phenomena: the doubling of differentially accessible peaks in XX PGCs from E12.5 to E13.5 and the massive increase in differentially accessible peaks in XY PGCs from E12.5 to E13.5. In our description of these results, we propose several hypotheses leading to these increases in differentially accessible peaks. As such, it cannot be ruled out that the changes to chromatin structure that occur during meiotic prophase I contribute to the gain in differentially accessible peaks in XX PGCs at E13.5, and we included this statement in the manuscript accordingly.

Reviewer #2 (Recommendations For The Authors):

(1) The methods state at line 141 that nuclei with mitochondrial reads of more than 25% were removed, however our understanding from the Bioconductor manual and companion manuscript (Amezquita, R.A., Lun, A.T.L., Becht, E. et al. Orchestrating single-cell analysis with Bioconductor. Nat Methods 17, 137-145 (2020). https://doi.org/10.1038/s41592-019-0654-x) is that snRNA-seq approaches remove mitochondrial transcripts entirely and datasets containing mitochondrial transcripts are thought to feature incompletely stripped nuclei. It is thought that mitochondrial transcripts participating in nuclear import may remain hanging on to the nuclear envelope and get encapsulated into GEMs. If the mitochondrial read cutoff of 25% was used intentionally to keep this potentially contaminating signal, please justify why this was done for this dataset.

We agree with the reviewer that the presence of mitochondrial transcripts may be potentially contaminating signal. In our preprocessing steps, we removed the mitochondrial genes and transcripts from our datasets so that they would not influence or affect our analyses. The following sentence was added to the methods section on snRNA-seq data processing: “Mitochondrial genes and transcripts were removed from the snRNA-seq datasets to eliminate any potentially contaminating signal.”

(2) Methods line 227: please include log2fold change and p-adjusted value cutoffs for GO enrichment.

We used clusterprofiler for our GO enrichment analysis. Our GO enrichment analysis did not include a log2fold change analysis and the p-adjusted value cutoff is stated in the methods.

(3) Results line 310: the claim that "At E12.5-E13.5, XY PGCs converged onto a single distinct population (cluster 7), indicating less transcriptional diversity among E12.5-E13.5 XY PGCs when compared to E12.5E13.5 XX PGCs (Fig1d)" would be strengthened if the authors quantified transcriptional distance with distance metrics such as euclidean or cosine distance.

We used a clustering approach to gain insights into the transcriptional diversity of PGC populations. Using an additional metric, such as Euclidean or cosine distance, would not provide meaningful information not already achieved by clustering or change the conclusions presented in the manuscript.

(4) Results line 317: the authors allude to Lars2 defining clusters 2 & 3 as a marker gene, but it is not clear why this is highlighted until the reader reaches the discussion, which alludes to the published role of Lars2 in reproduction. Please consider moving this sentence to the results section for clarity and perhaps expanding the discussion on the meaning.

To provide clarity, we added the statement “genes with reported roles in reproduction” to the results section.

(5) In Figure 2a, why do the authors choose to focus on Zkscan5 in XY PGCs when it is expressed by such a small portion of cells (<25%)? Do they assume that this is due to dropouts?

We chose to focus on Zkscan5 as an example because of its enriched and differential expression in male PGCs, the motif for Zkscan5 is not enriched in female PGCs, and the reported roles of Zkscan5 in regulating cellular proliferation and growth. Zkscan5 is an example of how candidate genes can be identified for further investigation.

(6) Line 461: "the population of E13.5 XX PGCs displaying the strongest Stra8 expression levels corresponded to the same population of XX PGCs with the highest module score of early meiotic prophase I genes (Figure 3c; Supplementary Fig. 3a-b)". However did the authors also consider examining the Stra8+ XX PGCs that do not robustly express meiotic genes to understand more about their differentiation potential?

We are thankful to the reviewer for this suggestion. However, this research question is beyond the scope of the manuscript. We plan to investigate further in future research studies.

(7) Line 505: "when we searched for the presence of RA receptor motifs in peaks linked to genes related to meiosis and female sex determination, we found that Stra8, Rec8, Rnf2, Sycp1, Sycp2, Ccnb3, and Zglp1 contain the RA receptor motifs in their regulatory sequences (Supplementary Figure 4g)." My read of the text is that the authors are not taking a side on the RA and meiosis controversy, but rather trying to reveal what the data can tell us, and the answer is that there is a strong signature linking RA to meiotic genes, which supports this as a valid biological pathway. But what is the strength of the RA>meiosis pathway compared to other mechanisms (which must be functioning in the triple receptor KO)? Perhaps the authors could take this analysis further with the following questions: (1) ask whether meiotic genes are more enriched in RA motifs compared to other expressed genes or other motifs (2) compare the strength of peak-gene correlations for all peaks containing RA receptor motifs vs. those with peaks for Zglp1, Rnf2, etc binding. The strengths of these correlations could provide clues to how much gene expression varies in response to RA exposure vs. modulation of these other factors and thus tell us something about how much RA is playing a role.

We agree with the reviewer that this is a very interesting and important question. We also thank the reviewer for their thoughtful suggestions on the types of bioinformatics analyses that could answer this question. However, the section on RA signaling during PGC sex determination is only a small part of the manuscript and would be better analyzed in greater detail in a future research study or publication.

(8) The shift from promoters in E11.5 XX PGCs to distal intergenic regions is fascinating. What can we learn about epigenetic reprogramming/methylation changes across gene bodies? 

We agree with the reviewer that this is an interesting question about gene regulation in E11.5 XX PGCs. However, we prefer to analyze the epigenetic reprogramming changes across gene bodies in this cell population in additional research studies. Our purpose and goal for this section was to link differentially accessible chromatin peaks with differentially expressed genes to identify putative gene regulatory networks.

(9) Line 581: why did the authors choose to highlight and validate PORCN1 in PGCs? Please elaborate.

As stated in the manuscript, we chose to highlight and validate PORCN1 in PGCs because of its role in WNT signaling and because of the visibly strong correlation between chromatin accessibility at the XXenriched DAP in Fig. 4c (dashed box) and and gene expression of PORCN1.

(10) Figure 5f would be easier to interpret if presented as two columns rather than a circle; show one line of the proteins and the other line with the transcripts so that each is on the same line and there are connections between them.

This comment is related to stylistic preferences. The purpose of Fig. 5f is to demonstrate that the candidate transcription factors may regulate the expression of other enriched transcription factors. Figure 5f figure accomplishes this goal.

(11) Line 640: "The predicted target genes of TCFL5 totaled 74% (367/494) of all DEGs with peak-to-gene linkages in XX PGCs". This seems like a high number and a lot of work for just TCFL5; given the overlap between other TFs and target genes, how many of these 367 target genes overlap with other TFs?

We agree with the reviewer that this is an important declaration to make. We added the following sentence to the results section on TCFL5: “A large majority of the predicted target genes of TCFL5 were also predicted to be the target genes of the enriched TFs presented in Fig. 5e, e.g., the predicted target genes of these TFs overlapped with 4%-100% of the predicted target genes of TCFL5.”

(12) The presentation of TCFL5 in the results section would make more sense with the additional mention of reproductive phenotypes already known (currently in the discussion Lines 914-917). I would furthermore suggest that the discussion goes into more depth on the difference between the regulatory network of TCFL5 in XX meiosis vs XY.

We thank the reviewer for this comment, however, we already state in the results section that TCFL5 is known to influence XX PGC sex determination.

(13) In the Methods, please state more clearly for those not familiar that the genetic background of mice is mixed.

We described the mice with their official names, which provides the context of their genetic backgrounds.

(14) Please specify which morphologic criteria were used to verify the stage of embryos in the methods.

We added the following text to the methods section of the revised manuscript: “Plug date was used to determine the stage of embryos collected for single-nucleus RNA-seq and ATAC-seq. The stage of E11.5 embryos was confirmed by counting somites. The stage of embryos collected at E12.5 was confirmed by the morphological presence of the vessel and cords of the testes collected from XY embryos. Similarly, we confirmed the stage of embryos collected at E13.5 by the size of the gonads, the presence of more distinct cords in the testes of XY embryos, and the elongation of the ovaries of XX embryos.”

(15) The total number of cells and PGCs that passed QC and are included in UMAPS should be stated.

The requested information was added to the legend for Fig. 1 of the revised manuscript: “The number of PGCs per sex and embryonic stage are: 375 E11.5 XX PGCs; 1,106 E12.5 XX PGCs; 750 E13.5 XX PGCs; 110 E11.5 XY PGCs; 465 E12.5 XY PGCs; and 348 E13.5 XY PGCs.”

(16) The order of timepoints changes between figures, and this is not for any obvious reason. Please make it consistent. Figures 1 and 6 list XX 11.5, 12.5, 13.5, and the same for XY, but Figures 2, 3, and 4 use the reverse order: XY E13.5, E12.5, E11.5, and then XX. 

We thank the reviewer for this comment. However, we chose this order for each of the figures to match the coordinates of the graphs and where we would expect the reader to begin reading the graph first. For example, in Figure 3a, XX E11.5 is closest to the x-axis and would be expected to be read first.   

(17) In Figure S2 the colors of clusters are hard to distinguish, and it is suggested that the cluster numbers should be listed above each colored bar to avoid frustration.

We made the suggested correction to Figure S2.

(18) In Figures 2e and 3e: what do the dashed boxes indicate?

The dashed boxes are to guide the reader’s eyes to the fact that the order of transcription factors/genes under the Cistrome DB regulatory potential score and gene expression plots are the same.

(19) In Figure 5a: break panels into i-iv so that the in-text call-outs are not all the same.

We made the suggested correction to Figure 5a and modified the in-text call-outs.

(20) Please indicate XX in Figure 5e and XY in Figure 5l.

We made the suggested correction to Figure 5e and 5l.

(21) In Figure S5c: Please reorganize DA chromatin peak charts so that columns are XX and XY with rows at the same timepoint.

We made the suggested correction to Figure S5c.

(22) In Figure S7a: please make images larger so that the overlapping expression of PORCN and TRA98 is more visible, and consider adding a more magnified panel.

This image is now included in the main text, with expanded panels.

(23) Line 742-754: this seems like a long introduction for the results section; please consider tightening it up.

We believe this text is important and necessary to provide context to the bioinformatics analyses of cell signaling pathways in PGCs. Not all readers will be familiar with the ligand-receptor signals between gonadal support cells and PGCs, and this text provides details on which signaling pathways are known to direct sex determination of PGCs.

(24) For UMAP plots in Figures 2c, 3c, S3b, and S4b, the text overlaid with the timepoints and sexes onto the UMAP plots is misleading, as it allows the reader to presume that the entire group of cells for a given sex/timepoint is located in the location of the text overlay. However, from the UMAP plots in Figure 1i-j, it is clear that the cells from a given sex/timepoint are actually spread across multiple identified clusters. Thus, the overlaid text obscures the important heterogeneity detected. To better represent the actual locations on the UMAP plot of cells from each sex/timepoint, it would be better to show inset density plots alongside these UMAP plots so the reader can locate the cells for themselves. 

We thank the reviewer for this comment. However, we chose this formatting to offer simplicity and ease of understanding to our UMAPs in addition to highlighting the general biological patterns of gene expression. If the reader is interested in discerning more of the heterogeneity of the UMAPs, they may refer back to Figure 1.

Reviewer #3 (recommendations for the authors):

There are some errors or places that need clarification or corrections:

(1) Figure 1f, according to the graph, it should be 8 clusters, not 9.

There are 9 clusters because the numbering for the clusters start at ‘0’.

(2) Why did cluster 8 have so many different states of cells from both sexes?

The identification of cluster 8 is likely an artifact of sequencing, and would require several different analyses to figure out why cluster 8 has many different states of cells from both sexes. While this will address a technical issue associated with the dataset, this will not change any major conclusions of the study.

(3) Figure 1i, shouldn't that be ten instead of eleven?

There are 11 clusters because the numbering for the clusters start at ‘0’.

(4) Figure 2a, zkscan expression level comparison was not so obvious as the bubble size was small. How many folds of differences from xx pgc?

There is a 1.5 fold increase in the expression of Zkscan5 between XY and XX PGCs at E13.5. We included this information in the revised manuscript.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors constructed a novel HSV-based therapeutic vaccine to cure SIV in a primate model. The novel HSV vector is deleted for ICP34.5. Evidence is given that this protein blocks HIV reactivation by interference with the NFkappaB pathway. The deleted construct supposedly would reactivate SIV from latency. The SIV genes carried by the vector ought to elicit a strong immune response. Together the HSV vector would elicit a shock and kill effect. This is tested in a primate model.

Strengths and weaknesses:

(1) Deleting ICP34.5 from the HSV construct has a very strong effect on HIV reactivation. The mechanism underlying increased activation by deleting ICP34.5 is only partially explored. Overexpression of ICP34.5 has a much smaller effect (reduction in reactivation) than deletion of ICP34.5 (strong activation); this is acknowledged by the authors that no full mechanistic explanation can be given at this moment.

Thank you for your comments. We agree with you that the mechanism underlying increased reactivation by deleting ICP34.5 is only partially explored. As you pointed out, the deletion of ICP34.5 leads to a significant reactivation, while the overexpression of ICP34.5 has a relatively weak inhibitory effect on reactivation. This difference prompts us to further contemplate the role of HSV-1 in regulating HIV latency and reactivation. Our data (Figure S4), along with previous literature (Mosca et al., 1987, Nabel et al., 1988), have indicated that the ICP0 protein might play a crucial role in the reactivation of HIV latency. However, we found for the first time that ICP34.5 can play an antagonistic role with this reactivation. This is a very interesting topic for understanding the complicated interactions between host cells and different viruses. We will investigate the deeper insights in future studies, and we have mentioned this limitation in the revised Discussion Section. Thank you!

(2) No toxicity data are given for deleting ICP34.5. How specific is the effect for HIV reactivation? A RNA seq analysis is required to show the effect on cellular genes.

A RNA seq analysis was done in the revised manuscript comparing the effect of HSV-1 and deleted vector in J-LAT cells (Fig S5). More than 2000 genes are upregulated after transduction with the modified vector in comparison with the WT vector. Hence, the specificity of upregulation of SIV genes is questioned. Authors do NOT comment on these findings. In my view it questions the utility of this approach.

Thank you for your mentions.

(1) As for the toxicity of HSV-ΔICP34.5, it is well known that ICP34.5 is a neurotoxicity factor that can antagonize host immune responses, and thus deleting ICP34.5 is beneficial to improve the safety of HSV-based constructs. As expected, we have demonstrated experimentally that HSV-DICP34.5 exhibited lower virulence and replication ability than wild-type HSV-1 (Figure S1). Importantly, we also observed a significant decrease in the expression of inflammatory factors in PWLH when compared to wild-type HSV-1 (Figure 1I-K). These data suggested that the safety of HSV-DICP34.5 should be more tolerable than wild-type HSV vector.

(2) The RNASeq analysis is aimed to explore the HSV-ΔICP34.5-induced signaling pathways, but it is not suitable to use this data for assessing the toxicity of HSV-ΔICP34.5 constructs. As for the RNASeq data, we think it is reasonable to observe many upregulated genes (which are involved in a variety of signaling pathways), since HSV-DICP34.5 constructs reactivated HIV latency more effectively than wild-type HSV by modulating the IKKα/β-NF-kB pathway and PP1-HSF1 pathway.

(3) To further validate whether HSV-ΔICP34.5 can specifically activate the HIV latent reservoir, we conducted additional experiments using vaccinia virus and adenovirus as controls, and results showed that both vaccinia virus and adenovirus cannot effectively reactivate HIV latency (Figure S3). Moreover, the deletion of ICP0 gene from HSV-1 diminished the reactivation effect of HIV latency by HSV-1, and overexpressing ICP0 greatly reactivate the latent HIV (Figure S4, Figure S5), implying that this reactivation should be virus-specific and ICP0 plays an important factor on reversing HIV latency. Interestingly, we herein found that ICP34.5 can act as an antagonistic factor for this reactivation of HIV latency by HSV-1. Thus, after the deletion of ICP34.5, the ability of HSV to reverse HIV latency was significantly enhanced. Our research group will investigate the underlying mechanism in future studies. Thank you for your insightful mention.

(3) The primate groups are too small and the results to variable to make averages. In Fig 5, the group with ART and saline has two slow rebounders. It is not correct to average those with the single quick rebounder. Here the interpretation is NOT supported by the data.

Although authors provided some promising SIV DNA data, no additional animals were added. Groups of 3 animals are too small to make any conclusion, especially since the huge variability in response. The average numbers out of 3 are still presented in the paper, which is not proper science.

No data are given of the effect of the deletion in primates. Now the deleted construct is compared with an empty vector containing no SIV genes. Authors provide new data in Fig S2 on the comparison of WT and modified vector in cells from PLWH, but data are not that convincing. A significant difference in reactivation is seen for LTR in only 2/4 donors and in Gag in 3/4 donors. (Additional question what is meaning of LTR mRNA, do authors relate to genomic RNA??)

Thank you for your serious review and kind reminder.

(1) We agree with you that it is not appropriated to use averages for this pilot study with limited numbers of macaques. We are currently unable to conduct another experiment with a larger number of macaques, but we think the results of this pilot study were very promising for further studies. Now, following your kind suggestions, we have removed the averages and now presented the data for each monkey individually in the revised manuscript. We have also modified the corresponding description accordingly (Line 254 to 262). Thank you for your understanding.

(2) Regarding your comment about the lack of data on the deletion of ICP34.5 from HSV-1, we are sorry for previously unclear description. In fact, the empty vector used in our animal experiments not only does not contain SIV antigens but also has the ICP34.5 deletion. We have revised the corresponding description accordingly (For example, we use HSV-DICP34.5DICP47-empty, HSV-DICP34.5DICP47-sPD1-SIVgag/SIVenv instead of HSV-empty, HSV-sPD1-SIVgag/SIVenv). We hope this revision will address your question.

(3) As for the reactivation effects observed in PLWH samples, the data may be not perfect, but we think this result (a significant difference in reactivation is seen for LTR in 2/4 donors and for Gag in 3/4 donors, and the purpose of detecting LTR RNA is to evaluate the level of virus replication) is promising to support our conclusion (The enhanced reactivation effect in primary CD4+ T cells by HSV-∆ICP34.5 than wild-type HSV). Of course, we recognize the need for more samples to gain a comprehensive understanding of reactivation effect in different individuals in future study. In addition, we corrected the description of LTR RNA (Lines 99-106 and 115-116). Thank you for the reminder!

Discussion

HSV vectors are mainly used in cancer treatment partially due to induced inflammation. Whether these are suitable to cure PLWH without major symptoms is a bit questionable to me and should at least be argued for.

The RNA seq data add on to this worry and should at least be discussed.

Thank you for your mention. As mentioned above, the RNASeq analysis is aimed to explore the HSV-ΔICP34.5-induced signaling pathways, but it is not suitable to use this data for assessing the toxicity of HSV-ΔICP34.5 constructs. Actually, ICP34.5 is a neurotoxicity factor that can antagonize innate immune responses, and thus ICP34.5 deletion is beneficial to improve the safety of HSV-based constructs. As expected, our data have demonstrated experimentally that HSV-DICP34.5 exhibited lower virulence and replication ability than wild-type HSV-1 (Figure S1). Importantly, HSV-DICP34.5 induced a lower level of inflammatory cytokines (including IL-6, IL-1β, and TNF-α) in primary CD4+ T cells from PLWH compared to HSV stimulation, likely due to its lower virulence and replication ability (Figure 1I-K). In addition, the CD4+ /CD8+ T cell ratio (Figure 5H) and body weight (Figure S10) after treatment were effectively ameliorated in the SIV-infected macaques of the ART+HSV-DICP34.5DICP47-sPD1-SIVgag/SIVenv group. Our data also demonstrated that there was no significant effect on the cell composition of peripheral blood in the SIV-infected macaques of ART+HSV-DICP34.5DICP47-sPD1-SIVgag/SIVenv group (Figure S11). These data suggested that the safety of HSV-DICP34.5 should be more tolerable than wild-type HSV vector. We have added a more comprehensive description in the revised Discussion (Lines 328-334). Thank you again for all of your kind comments and suggestions.

Reviewer #2 (Public review):

Summary:

In this article Wen et. al., describe the development of a 'proof-of-concept' bi-functional vector based out of HSV-deltaICP-34.5's ability to purge latent HIV-1 and SIV genomes from cells. They show that co-infection of latent J-lat T-cell lines with a HSV-deltaICP-34.5 vector can reactivate HIV-1 from a latent state. Over- or stable expression of ICP 34.5 ORF in these cells can arrest latent HIV-1 genomes from transcription, even in the presence of latency reversal agents. ICP34.5 can co-IP with- and de-phosphorylate IKKa/b to block its interaction with NF-k/B transcription factor. Additionally, ICP34.5 can interact with HSF1 which was identified by mass-spec. Thus, the authors propose that the latency reversal effect of HSV-deltaICP-34.5 in co-infected JLat cells is due to modulatory effects on the IKKa/b-NF-kB and PP1-HSF-1 pathway.

Next the authors cleverly construct a bifunctional HSV based vector with deleted ICP34.5 and 47 ORFs to purge latency and avoid immunological refluxes, and additionally expand the application of this construct as a vaccine by introducing SIV genes. They use this 'vaccine' in mouse models and show the expected SIV-immune responses. Experiments in rhesus macaques (RM), further elicit potential for their approach to reactivate SIV genomes and at the same time block their replication by antibodies. What was interesting in the SIV experiments is that the dual-functional vector vaccine containing sPD1- and SIV Gag/Env ORFs effectively delayed SIV rebound in RMs and in some cases almost neutralized viral DNA copy detection in serum. Very promising indeed, however there are some questions I wish the authors explored to answer, detailed below.

Overall, this is an elegant and timely work demonstrating the feasibility of reducing virus rebound in animals, and potentially expand to clinical studies. The work was well written, and sections were clearly discussed.

Strengths:

The work is well designed, rationale explained and written very clearly for lay readers.

Claims are adequately supported by evidence and well designed experiments including controls.

We appreciate your positive comment for our work.

Weaknesses:

(1) It looks like ICP0 is also involved in latency reversal effects. More follow-up work will be required to test if this is in fact true.

Both our data (Figure S4, Figure S5) and previous literature (Nabel et al., 1988, Mosca et al., 1987) have reported that HSV ICP0 may play a role in reversing HIV latency. However, the exact mechanisms behind this effect have not yet been fully elucidated. Of note, we herein reported for the first time that ICP34.5 can act as an antagonistic factor for this reactivation of HIV latency by HSV-1. Thus, after the deletion of ICP34.5, the ability of HSV to reverse HIV latency was significantly enhanced. Our research group will investigate the underlying mechanism in future studies. Thank you for your insightful mention.

(2) It is difficult to estimate the depletion of the latent viral reservoir. The authors have tried to address this issue. A more convincing argument to this reviewer will be data to demonstrate that after the bi-functional vaccine, the animals show overall reduction in the number of circulating latent cells. The feasibility to obtain such a result is not clearly demonstrated.

Thank you for your comment. As you mentioned, we have indeed measured both total DNA and integrated DNA (iDNA) in blood cells (see Figure 5E-F), which can provide support for the reduction of the latent viral reservoir. Thank you for your kind reminder.

(3) The authors state that the reduced virus rebound detected following bi-functional vaccine delivery is due to latent genomes becoming activated and steady-state neutralization of these viruses by antibody response. This needs to be demonstrated. Perhaps cell-culture experiments from specimen taken from animals might help address this issue. In lab cultures one could create environments without antibody responses, under these conditions one would expect higher level of viral loads being released in response to the vaccine in question.

Thank you for your valuable suggestion. We believe that the reduced virus rebound observed may be influenced by immune responses from T cells and antibodies induced by both ART and the vaccine. We appreciate your insight and agree that future studies should focus on investigating the activation effects of the vaccine under controlled conditions that simulate the absence of immune responses in primary animal cells. This will help us better understand the mechanisms involved and address your concerns more comprehensively.

Reviewer #2 (Recommendations for the authors):

The Authors have sufficiently addressed my comments. Below are a few minor changes that can help with clarity.

Lines 126-127: This sentence should be changed. Perhaps, "these data suggests that .... Safety of... in PLWH might be tolerable, at least in vitro."

Thanks for your suggestion. We have revised it accordingly. (Line 130).

Lines 128-132: Would this not mean that reactivation is due to ICP0 gene? Have the authors tried to express ICP0-gene into J-Lat cells and see if that is the reason for reactivation? This seems somewhat incomplete. At the end of 132, please add ", in the presence of ICP0". Also a sentence describing this effect is warranted.

Thank you for your insightful suggestion. Yes, both our data and previous literature supported that the ICP0 gene can play a significant role in the reactivation of HIV latency (Figure S4, Figure S5). Of note, we herein reported for the first time that ICP34.5 can act as an antagonistic factor for this reactivation of HIV latency by HSV-1. Thus, after the deletion of ICP34.5, the ability of HSV to reverse HIV latency was significantly enhanced. We have described this effect in the revised version accordingly. Additionally, we have added the phrase “in the presence of ICP0” to the results section (Lines 137) to clarify this point.

MOSCA, J. D., BEDNARIK, D. P., RAJ, N. B., ROSEN, C. A., SODROSKI, J. G., HASELTINE, W. A., HAYWARD, G. S. & PITHA, P. M. 1987. Activation of human immunodeficiency virus by herpesvirus infection: identification of a region within the long terminal repeat that responds to a trans-acting factor encoded by herpes simplex virus 1. Proc Natl Acad Sci U S A 84:  7408.DOI: https://doi.org/10.1073/pnas.84.21.7408, PMID: 2823260

NABEL, G. J., RICE, S. A., KNIPE, D. M. & BALTIMORE, D. 1988. Alternative mechanisms for activation of human immunodeficiency virus enhancer in T cells. Science 239:  1299.DOI: https://doi.org/10.1126/science.2830675, PMID: 2830675

Author response:

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

Reviewer #1 (Public Review):

Summary:

By using the biophysical chromosome stretching, the authors measured the stiffness of chromosomes of mouse oocytes in meiosis I (MI) and meiosis II (MII). This study was the follow-up of previous studies in spermatocytes (and oocytes) by the authors (Biggs et al. Commun. Biol. 2020: Hornick et al. J. Assist. Rep. and Genet. 2015). They showed that MI chromosomes are much stiffer (~10 fold) than mitotic chromosomes of mouse embryonic fibroblast (MEF) cells. MII chromosomes are also stiffer than the mitotic chromosomes. The authors also found that oocyte aging increases the stiffness of the chromosomes. Surprisingly, the stiffness of meiotic chromosomes is independent of meiotic chromosome components, Rec8, Stag3, and Rad21L. with aging.

Strengths:

This provides a new insight into the biophysical property of meiotic chromosomes, that is chromosome stiffness. The stiffness of chromosomes in meiosis prophase I is ~10-fold higher than that of mitotic chromosomes, which is independent of meiotic cohesin. The increased stiffness during oocyte aging is a novel finding.

Weaknesses:

A major weakness of this paper is that it does not provide any molecular mechanism underlying the difference between MI and MII chromosomes (and/or prophase I and mitotic chromosomes).

We acknowledge that our study does not provide a comprehensive explanation for the stage-related alterations in chromosome stiffness; however, we believe that the observation of these changes is itself of broad interest. Initially, we hypothesized that DNA damage or depletion of meiosis-specific cohesin might contribute to the observed increase in chromosome stiffness. However, our experimental finding did not support these hypotheses, indicating that neither DNA damage nor cohesion depletion is responsible for the stiffness increase. The molecular basis underlying the stage-related stiffness increase remains elusive and requires exploration in future studies. In the Discussion, we propose that factors such as condensin, nuclear proteins, and histone methylation may play a role in regulating meiotic chromosome stiffness. The involvement of these factors in stage-related chromosome stiffening requires future investigation.

Reviewer #2 (Public Review):

This paper reports investigations of chromosome stiffness in oocytes and spermatocytes. The paper shows that prophase I spermatocytes and MI/MII oocytes yield high Young Modulus values in the assay the authors applied. Deficiency in each one of three meiosis-specific cohesins they claim did not affect this result and increased stiffness was seen in aged oocytes but not in oocytes treated with the DNA-damaging agent etoposide.

The paper reports some interesting observations which are in line with a report by the same authors of 2020 where increased stiffness of spermatocyte chromosomes was already shown. In that sense, the current manuscript is an extension of that previous paper, and thus novelty is somewhat limited. The paper is also largely descriptive as it does neither propose a mechanism nor report factors that determine the chromosomal stiffness.

There are several points that need to be considered.

(1) Limitations of the study and the conclusions are not discussed in the "Discussion" section and that is a significant gap. Even more so as the authors rely on just one experimental system for all their data - there is no independent verification - and that in vitro system may be prone to artefacts.

Our experimental system has been used to study different types of chromosome stiffness as well as nuclear stiffness.  We have compared our results with previously published data and found the data is consistent across different experiments. To address the reviewer’s concern, we describe the limitations of our in vitro experimental approach in the Discussion section.

(2) It is somewhat unfortunate that they jump between oocytes and spermatocytes to address the cohesin question. Prophase I (pachytene) spermatocytes chromosomes are not directly comparable to MI or MII oocyte chromosomes. In fact, the authors report Young Modulus values of 3700 for MI oocytes and only 2700 for spermatocyte prophase chromosomes, illustrating this difference. Why not use oocyte-specific cohesin deficiencies?

In this study, our goal was to investigate the mechanism underlying the increased chromosome stiffness observed during prophase I. Ideally, we would have compared wild-type and cohesin-deleted mouse oocytes at the metaphase I (MI) stage. However, experimental constraints made this approach unfeasible: spermatocytes and oocytes from  Rec8^-/- and  Stag3^-/- mutant mice cannot reach MI stage, and  Rad21l^-/- mutant mice are sterile in males and subfertile in females, because cohesin proteins are crucial for germline cell development.

Additionally, collecting prophase I chromosomes from oocytes is exceptionally challenging and requires fetal mice as prophase I oocyte sources because female oocytes progress to the diplotene stage during fetal development. The process is further complicated by the difficulty of genotyping fetal mice, making the study of female prophase I impracticable. By contrast, spermatocytes are continuously generated in males throughout life, with meiotic stages readily identifiable, making them more accessible for analysis.

Our findings consistently showed increased chromosome stiffness in both prophase I spermatocytes and MI oocytes, suggesting that the phenomenon is not sex-specific. This observation implies that similar effects on chromosome stiffness may occur across meiotic stages, from prophase I to MI.

(3) It remains unclear whether the treatment of oocytes with the detergent TritonX-100 affects the spindle and thus the chromosomes isolated directly from the Triton-lysed oocytes. In fact, it is rather likely that the detergent affects chromatin-associated proteins and thus structural features of the chromosomes.

Regarding the use of Triton X-100, it is important to emphasize that the concentration used (0.05%) is very low and unlikely to significantly affect chromosome stiffness. To support this assertion, we have provided additional evidence in the revised manuscript demonstrating that this low concentration of Triton X-100 has a negligible effect on chromosome stiffness (Supplement Fig. 5, Right panel).

(4) Why did the authors use mouse strains of different genetic backgrounds, CD-1, and C57BL/6? That makes comparison difficult. Breeding of heterozygous cohesin mutants will yield the ideal controls, i.e. littermates.

The genetic mutant mice, all in a C57BL/6 background, were generously provided by Dr. Philip Jordan and delivered to our lab. As our lab does not currently maintain C57BL/6 colony and given that this strain typically produces small litter sizes - which would have complicated the remainder of the study - we chose CD-1 mice as the control group and used C57BL/6 mice specifically for the cohesin study. To address potential concerns regarding genetic background differences, we compared our results with previously published data from C57BL/6 mice and found no significant differences (2710 ± 610 Pa versus 3670 ± 840 Pa, P= 0.4809) (Biggs et al., 2020). Furthermore, prophase I spermatocytes from CD-1 mice showed no significant difference compared to any of the three cohesin-deleted C57BL/6 mutant mice, suggesting that chromosome stiffness is not significantly influenced by genetic background.

(5) How did the authors capture chromosome axes from STAG3-deficienct spermatocytes which feature very few if any axes? How representative are those chromosomes that could be captured?

We isolated chromosomes from prophase I mutant spermatocytes, which were identified by their large size, round shape, and thick chromosomal threads - characteristics indicative of advanced condensation and a zygotene-like stage during prophase I (Supplemental Fig. 3). The methodology for isolating these chromosomes has been described in details in our previous publication (Biggs et al., 2020), which is referenced in the current manuscript.

Reviewer #3 (Public Review):

Summary:

Understanding the mechanical properties of chromosomes remains an important issue in cell biology. Measuring chromosome stiffness can provide valuable insights into chromosome organization and function. Using a sophisticated micromanipulation system, Liu et al. analyzed chromosome stiffness in MI and MII oocytes. The authors found that chromosomes in MI oocytes were ten-fold stiffer than mitotic ones. The stiffness of chromosomes in MI mouse oocytes was significantly higher than that in MII oocytes. Furthermore, the knockout of the meiosis-specific cohesin component (Rec8, Stag3, Rad21l) did not affect meiotic chromosome stiffness. Interestingly, the authors showed that chromosomes from old MI oocytes had higher stiffness than those from young MI oocytes. The authors claimed this effect was not due to the accumulated DNA damage during the aging process because induced DNA damage reduced chromosome stiffness in oocytes.

Strengths:

The technique used (isolating the chromosomes in meiosis and measuring their stiffness) is the authors' specialty. The results are intriguing and informative to the chromatin/chromosome and other related fields.

Weaknesses:

(1) How intact the measured chromosomes were is unclear.

Currently, a well-calibrated chromosome mechanics experiment requires the extracellular isolation of chromosomes. In experiments conducted parallel to those in our previous study (Biggs et al., 2020), we obtained quantitatively consistent results, including measurements of the Young modulus for prophase I spermatocyte chromosomes.  Our isolation approach is significantly gentler than bulk methods that rely on hypotonic buffer-driven cell lysis and centrifugation. If substantial chromosomal damage had occurred during isolation, we would expect greater variation between experiments, as different amounts or types of damage could influence the results. 

(2) Some control data needs to be included.

We used wild-type prophase I spermatocytes and metaphase I (MI) oocytes as controls. To validate our findings, we compared some of our results with those reported in a previous study and observed consistent outcomes (Biggs et al., 2020).

(3) The paper was not well-written, particularly the Introduction section.

We have revised the paper and improved the overall quality of the manuscript.

(4) How intact were the measured chromosomes? Although the structural preservation of the chromosomes is essential for this kind of measurement, the meiotic chromosomes were isolated in PBS with Triton X-100 and measured at room temperature. It is known that chromosomes are very sensitive to cation concentrations and macromolecular crowding in the environment (PMID: 29358072, 22540018, 37986866). It would be better to discuss this point.

As suggested, we investigated the impact of PBS and Triton X-100 on chromosome stiffness. Our findings indicate that neither PBS nor Triton X-100 caused significant changes in chromosome stiffness (Supplemental Fig. 5).

Recommendations For The Authors:

Major points of Reviewers that the Editor indicated should be addressed

(1) Reviewer's point 3, the effect of the high concentration of etoposide: It would be advisable to use lower concentrations of etoposide to observe the effect of DNA damage on chromosome stiffness more accurately.

The effect of etoposide on oocyte is dose-dependent (Collins et al., 2015). Oocytes are generally not highly sensitive to DNA damage, and even at relatively high concentrations, not all may exhibit a response. To ensure that sufficient DNA damage in the oocytes we isolated, we used relatively high concentration of etoposide for the experiment. This concentration (50 μg/ml) falls within the typical range reported in the literature (Marangos and Carroll, 2012)(Cai et al., 2023)(Lee et al., 2023). As the reviewer suggested, we tested two additional lower concentrations of etoposide (5 μg/ml and 25 μg/ml) (see Fig. 5 C). We did not observe any significant differences in chromosome stiffness in 5 µg/ml etoposide-treated oocytes compared to the control. However, higher concentrations of etoposide (25 μg/ml) significantly reduced oocyte chromosome stiffness compared to the control.

Revision to manuscript:

“Results at lower etoposide concentrations revealed that chromosome stiffness in untreated control oocytes was not significantly different from that in oocytes treated with 5 μg/ml etoposide (3780 ± 700 Pa versus 3930 ± 400 Pa, P = 0.8624). However, chromosome stiffness in untreated oocytes was significantly higher than that in oocytes treated with 25 μg/ml etoposide (3780 ± 700 Pa versus 1640 ± 340 Pa, P = 0.015) (Figure 5C).”

(2) Reviewer's point 3, the effect of Triton X-100: This is related to the concern of the #3 reviewer. It is critical to check whether the detergent does not affect the stiffness indirectly or not.

To demonstrate that the low concentration of Triton X-100 does not influence chromosome stiffness, we conducted additional experiments. First, we isolated chromosomes and measured their stiffness. Then, we treated the chromosomes with 0.05% Triton X-100 via micro-spraying and remeasured the stiffness. The results showed no significant difference (see Supplement Fig. 5 right panel).

Revision to manuscript:

“In addition to past experiments indicating that mitotic chromosomes are stable for long periods after their isolation (Pope et al., 2006), we carried out control experiments on mouse oocyte chromosomes where we incubated them for 1 hour in PBS, or exposed them to a flow of Triton X-100 solution for 10 minutes; there was no change in chromosome stiffness in either case (Methods and Supplementary Fig. 5).”

(3) Reviewer's point 1, the effect of the buffer composition: Please describe how the composition affects the stiffness of the chromosomes.

PBS is an economical and effective buffer solution that closely mimics the osmotic conditions of the cytoplasm, which is crucial for maintaining chromosomal structural integrity. Appropriate ion concentrations are crucial for preserving chromosome integrity, as imbalances—either too high or too low—can alter chromosome morphology (Poirier and Marko, 2002). When chromosomes are stored in PBS, their stiffness remains relatively stable, even with prolonged exposure, ensuring minimal changes to their physical properties. To confirm this, we isolated chromosomes and measured their stiffness. After one-hour incubation in PBS, we remeasured stiffness and observed no significant differences, which demonstrated that chromosomes remain stable in PBS (see Supplement Fig.5 left panel).

Revision to manuscript:

“In this study, we developed a new way to isolate meiotic chromosomes and measure their stiffness. However, one concern is that the measurements were conducted in PBS solution, which is different from the intracellular environment. To address this, we monitored chromosome stiffness overtime in PBS solution and found that it remained stable over a period of one hour (Supplement Fig. 5 Left panel).”

Reviewer #1 (Recommendations For The Authors):

Major points:

(1) Previously, the role of condensin complexes in chromosome stiffness is shown (Sun et al. Chromosome Research, 2018). Thus, at least the authors described the condensin staining on MI and MII chromosomes.

We have added sentences in the discussion to elaborate on the role of condensin.

Revision to manuscript:

“Several factors, including condensin, have been found to affect chromosome stiffness (Sun et al., 2018). Condensin exists in two distinct complexes, condensin I and condensin II, and both are active during meiosis. Published studies indicate that condensin II is more sharply defined and more closely associated with the chromosome axis from anaphase I to metaphase II (Lee et al., 2011). Additionally, condensin II appears to play a more significant role in mitotic chromosome mechanics compared to condensin I (Sun et al., 2018). Thus, condensin II likely contributes more significantly to meiotic chromosome stiffness than condensin I.”

(2) Although the authors nicely showed the difference in the stiffness between MI and MII chromosomes (Figure 2), as known, MI chromosomes are bivalent (with four chromatids) while MII chromosomes are univalent (with two chromatids). The physical property of the chromosomes would be affected by the number of chromatids. It would be essential for the authors to measure the physical properties of a univalent of MI chromosomes from mice defective in meiotic recombination such as Spo11 and/or Mlh3 KO mice.

The reviewer correctly pointed out that the number of chromatids in chromosomes differs between metaphase I (MI) and metaphase II (MII) stages. We have addressed this difference by calculating Young’s modulus (E), a mechanical property that describes the elasticity of a material, independent of its geometry. Young’s modulus describes the intrinsic properties of the material itself, rather than the specific characteristics of the object being tested. It is calculated as E=(F/A)/(∆L/L0), where F was the force given to stretch the chromosome, A was the cross-section area, ∆L was the length change of the chromosome, and L0 was the original length of the chromosome. While an increase in chromosome or chromatid numbers, results in a larger cross-sectional area, leading to a higher doubling force (F). This variation in chromosome number or cross-sectional area does not impact the calculation of chromosome stiffness/Young’s modulus (E). While study of the mutants suggested by the referee would certainly be interesting, it would be likely that the absence of these key recombination factors would impact chromosome stiffness in a more complex way than just changing their thickness; this type of study is beyond the scope of the present manuscript and is an exciting direction for future studies.

(3) In Figure 5, the authors measure the stiffness of etoposide-treated MI chromosomes. The concentration of the drug was 50 ug/ml, which is very high. The authors should analyze the different concentrations of the drug to check the chromosome stiffness. Moreover, etoposide is an inhibitor of Topoisomerase II. The effect of the drug might be caused by the defective Top2 activity, rather than Top2-adducts, thus DNA damage. It is very important to check the other Top2 inhibitors or DNA-damaging agents to generalize the effect of DNA damage on chromosome stiffness. Moreover, DNA damage induces the DNA damage response. It is important to check the effect of DDR inhibitors on the damage-induced change of stiffness.

The reviewer is correct in noting that etoposide can induce DNA damage and inhibit Top2 activity. To address this concern, our previous DNase experiment provided further clarity and supports our results of this study (Biggs et al., 2020). This experiment was conducted in vitro, where DNase treatment caused DNA damage on chromosomes without affecting Top2 activity or triggering DNA damage response. The results demonstrated that DNase treatment led to reduced chromosome stiffness, which aligns with the findings presented in our manuscript.

(4) In the same line as the #3 point, the authors also need to check the effect of etoposide on the stiffness of mitotic chromosomes from MEF.

Experiments on MEF mitotic chromosomes were designed to serve as a reference for the meiotic chromosome studies. The etoposide experiments on meiotic chromosomes specifically aimed to investigate how DNA damage affects meiotic chromosome structure. While it would be interesting to explore the effects of etoposide-induced DNA damage on mitotic chromosomes, it represents a distinct research question that falls outside the scope of the current study.

Minor points:

(1) Line 141-142: Previous studies by the author analyzed the stiffness of mitotic chromosomes from pro-metaphase. Which stage of cell cycles did the authors analyze here?

To ensure consistency in our experiments, we also measured the stiffness of mitotic chromosomes at the prometaphase stage. The precise stage used is very near to metaphase, at the very end of the prometaphase stage. We have modified the manuscript to clarify this point.

Revision to manuscript:

“For comparison with the meiotic case, we measured the chromosome stiffness of Mouse Embryonic Fibroblasts (MEFs) at late pro-metaphase (just slightly before their attachment to the mitotic spindle) and found that the average Young’s modulus was 340 ± 80 Pa (Figure 2B). The value is consistent with our previously published data, where the modulus for MEFs was measured to be 370 ± 70 Pa (Biggs et al., 2020).”

(2) Line 157: Here, the doubling force of MI (and MII) oocytes should be described in addition to those of spermatocytes.

The purpose of this paragraph is to demonstrate the reproductivity and consistency of our experiments. In this section, we compared our data with previously published findings. Published data do not include chromosome stiffness measurement from MI mouse oocytes. Our experiment is the first to assess this. Therefore, we did not include MI mouse oocytes in that comparison. To clarify this, we have added sentences to highlight the comparison of doubling force.

Revision to manuscript:

“Here, we found that the doubling forces of chromosomes from MI and MII oocytes are 3770 ± 940 pN and 510 ± 50 pN, respectively. We conclude that chromosomes from MI oocytes are much stiffer than those from both mitotic cells and MII oocytes (Supplement Fig. 2), in terms of either Young’s modulus or doubling force.”

(3) Line 202: What stage of prophase I do the authors mean by the spermatocyte stage here? Diakinesis, Metaphase I or prometaphase I? I am not sure how the authors can determine a specific stage of prophase I by only looking at the thickness of the chromosomes. Please show the thickness distribution of WT and Rec8^-/- chromosomes.

We have reworded the sentence and clarified that the spermatocyte stage is prophase I stage. Since Rec8^-/- spermatocytes cannot progress beyond the pachytene stage of prophase I, the isolated chromosomes must be in prophase I rather than diakinesis, metaphase I, prometaphase I, or any later stages (Xu et al., 2005). Based on the cell size and degree of chromosome condensation (Biggs et al., 2020), it is most likely that the measured chromosomes are at the zygotene-like stage. However, as we cannot definitively determine the exact substage of prophase I, thus, we have referred to them simply as prophase I.

Revision to manuscript:

“We isolated chromosomes from Rec8^-/- prophase I spermatocytes, which displayed large and round cell size and thick chromosomal threads, indicative of advanced chromosome compaction after stalling at a zygotene-like prophase I stage (Supplement Fig. 3). The combination of large cell size and degree of chromosome compaction allowed us to reliably identify Rec8^-/- prophase I chromosomes. Using micromanipulation, we measured chromosome stiffness by stretching the chromosomes (Supplement Fig. 3) (Biggs et al., 2019).”

Reviewer #2 (Recommendations For The Authors):

(1) Line 135: that statement is not substantiated; better to show retraction data and full reversibility.

We added a figure showing oocyte chromosome stretching, which showed that the oocyte chromosome is elastic, and that the stretching process is reversible (Supplement Fig.1).

(2) Line 144: the authors claim that the Young Modulus of MII oocytes is "slightly" higher than that of mitotic cells (MEFs). Well, "slightly" means it is rather similar, and therefore the commonly used statement that MII is similar to mitosis is OK - contrary to the authors' claim.

We have removed the word “slightly” in the manuscript. The difference is statistically significant.

Revision to manuscript:

“Surprisingly, despite this reduction, the stiffness of MII oocyte chromosomes was still significantly higher than that for mitotic cells (Figure 2B).”

(3) There are a lot of awkward sentences in this text. Some sentences lack words, are not sufficiently precise in wording and/or logic, and there are numerous typos. Some examples can be found in lines 89 (grammar), 94, 95 ("looked"), 98, 101 ("difference" - between what?), and some are commonplaces or superficial (lines 92/93, 120..., ). Occasionally the present and past tense are mixed (e.g. in M&M). Thus the manuscript is quite poorly written.

Thanks for the comments of the reviewer. We have revised all the sentences highlighted by the reviewer and polished the entire manuscript.

Reviewer #3 (Recommendations For The Authors):

(1) Line 48. "We then investigated the contribution of meiosis-specific cohesin complexes to chromosome stiffness in MI and MII oocytes." There is no data on oocytes with meiosis-specific cohesin KO. This part should be corrected.

We have corrected this error.

Revision to manuscript:

“We examined the role of meiosis-specific cohesin complexes in regulating chromosome stiffness.”

(2) Lines 155-157. The result of MI mouse oocyte chromosomes should also be mentioned here (Supplementary Figure 1).

Please see our response to Reviewer 1 – Minor Point 2.

(3) Line 163. "The stiffness of chromosomes in MI mouse oocytes is significantly higher compared to MII oocytes."<br /> Is this because two homologs are paired in MI chromosomes (but not in MII chromosomes)? The authors may want to discuss the possible mechanism.

Please see our response to Reviewer 1 – Major Point 2.

(4) Line 188: "We hypothesized that MI oocytes... would have higher chromosome stiffness than MII oocytes." Why did the authors measure chromosomes from spermatocytes but not MI oocytes?

Both spermatocytes and oocytes from Rec8^-/-, Stag3^-/-, and Rad21l^-/- mutant mice cannot reach MI stage because cohesin proteins are crucial for germline-cell development. We chose to use spermatocytes in our study because collecting fetal meiotic oocytes is extremely difficult, and genotyping fetal mice adds another layer of complexity to the experiments. In females, all oocytes complete prophase I and progress to the dictyotene stage during the fetal stage. Obtaining individual oocytes at this stage is challenging. In contrast, spermatocytes are continuously generated at all stages in males.

(5) To support the authors' conclusion, verifying the KO of REC8, STAG3, and RAD21L by immunostaining or other methods is essential.

These mice are provided by one of the authors, Dr. Philip Jordan, who has published several papers using these knockout mice (Hopkins et al., 2014)(Ward et al., 2016). The immunostaining of these models has already been well-characterized in those previous studies. In addition to performing double genotyping, we also use the size of the collected testes as an additional verification of the mutant genotype. These knockout mice have significantly smaller testes compared to their wild-type counterparts, providing a clear physical indicator of the mutation.

(6) Some of the cited papers and descriptions in the Introduction are not appropriate and confusing. This part should be improved:

Line 79. Recent studies have revealed that the 30-nm fiber is not considered the basic structure of chromatin (e.g., review, PMID: 30908980; original papers, PMID: 19064912, 22343941, 28751582). This point should be included.

We have corrected the references as needed. Additionally, thank you for the updated information regarding the 30-nm fiber. We have removed all the descriptions about the 30-nm fiber to ensure the information is accurate and up to date.

(7) Line 83. Reviews on mitotic chromosomes, rather than Ref. 9, should be cited here. For instance, PMID: 33836947, 31230958.

We have corrected it and added references according to the review’s suggestion.

(8) Line 85. Refs. 10 and 11 are not on the "Scaffold/Radial-Loop" model. For instance, PMID: 922894, 277351, 12689587. The other popular model is the hierarchical helical folding model (PMID: 98280, 15353545).

We have corrected it and added appropriate references according to the review’s suggestion. Regarding the hierarchical helical folding model, our experiments do not provide data that either support or refute this model. Thus, we have opted not to include any discussion of this model in our manuscript.

(9) Figure legends. There is no description of the statistical test.

We have added the description of the statistical test at the end of the figure legends for clarity.

(10) Line 156. The authors should mention which stages in spermatocyte prophase I (pachytene?) were used for their measurement.

We cannot precisely determine the substage of prophase I in the spermatocytes although it is most likely in the pachytene stage.

(11) Line 241. "DNA damage reduces chromosome stiffness in oocytes." It would be better to show how much damage was induced in aged and etoposide-treated chromosomes, for example, by gamma-H2AX immunostaining. In addition, there are some papers that show DNA damage makes chromatin/chromosomes softer (e.g., PMID: 33330932). The authors need to cite these papers.

The effects of etoposide and age on meiotic oocytes has been published (Collins et al., 2015)(Marangos et al., 2015)(Winship et al., 2018).

We are grateful for the citation information provided by the reviewer and have added it to our manuscript.

Revision to manuscript:

“Overall, these findings suggest that DNA damage reduces chromosome stiffness in oocytes instead of increasing it, which aligns with other studies showing that DNA damage can make chromosomes softer (Dos Santos et al., 2021). These results suggest that the increased chromosome stiffness observed in aged oocytes is not due to DNA damage.”

(12) Line 328. Senescence?

This error is corrected in the revised manuscript.

Revision to manuscript:

“Defective chromosome organization is often related to various diseases, such as cancer, infertility, and senescence (Thompson and Compton, 2011; Harton and Tempest, 2012; He et al., 2018).”

References:

Biggs, R., P.Z. Liu, A.D. Stephens, and J.F. Marko. 2019. Effects of altering histone posttranslational modifications on mitotic chromosome structure and mechanics. Mol. Biol. Cell. 30:820–827. doi:10.1091/mbc.E18-09-0592.

Biggs, R.J., N. Liu, Y. Peng, J.F. Marko, and H. Qiao. 2020. Micromanipulation of prophase I chromosomes from mouse spermatocytes reveals high stiffness and gel-like chromatin organization. Commun. Biol. 3:1–7. doi:10.1038/s42003-020-01265-w.

Cai, X., J.M. Stringer, N. Zerafa, J. Carroll, and K.J. Hutt. 2023. Xrcc5/Ku80 is required for the repair of DNA damage in fully grown meiotically arrested mammalian oocytes. Cell Death Dis. 14:1–9. doi:10.1038/s41419-023-05886-x.

Collins, J.K., S.I.R. Lane, J.A. Merriman, and K.T. Jones. 2015. DNA damage induces a meiotic arrest in mouse oocytes mediated by the spindle assembly checkpoint. Nat. Commun. 6. doi:10.1038/ncomms9553.

Harton, G.L., and H.G. Tempest. 2012. Chromosomal disorders and male infertility. Asian J. Androl. 14:32–39. doi:10.1038/aja.2011.66.

He, Q., B. Au, M. Kulkarni, Y. Shen, K.J. Lim, J. Maimaiti, C.K. Wong, M.N.H. Luijten, H.C. Chong, E.H. Lim, G. Rancati, I. Sinha, Z. Fu, X. Wang, J.E. Connolly, and K.C. Crasta. 2018. Chromosomal instability-induced senescence potentiates cell non-autonomous tumourigenic effects. Oncogenesis. 7. doi:10.1038/s41389-018-0072-4.

Hopkins, J., G. Hwang, J. Jacob, N. Sapp, R. Bedigian, K. Oka, P. Overbeek, S. Murray, and P.W. Jordan. 2014. Meiosis-Specific Cohesin Component, Stag3 Is Essential for Maintaining Centromere Chromatid Cohesion, and Required for DNA Repair and Synapsis between Homologous Chromosomes. PLoS Genet. 10:e1004413. doi:10.1371/journal.pgen.1004413.

Lee, C., J. Leem, and J.S. Oh. 2023. Selective utilization of non-homologous end-joining and homologous recombination for DNA repair during meiotic maturation in mouse oocytes. Cell Prolif. 56:1–12. doi:10.1111/cpr.13384.

Lee, J., S. Ogushi, M. Saitou, and T. Hirano. 2011. Condensins I and II are essential for construction of bivalent chromosomes in mouse oocytes. Mol. Biol. Cell. 22:3465–3477. doi:10.1091/mbc.E11-05-0423.

Marangos, P., and J. Carroll. 2012. Oocytes progress beyond prophase in the presence of DNA damage. Curr. Biol. 22:989–994. doi:10.1016/j.cub.2012.03.063.

Marangos, P., M. Stevense, K. Niaka, M. Lagoudaki, I. Nabti, R. Jessberger, and J. Carroll. 2015. DNA damage-induced metaphase i arrest is mediated by the spindle assembly checkpoint and maternal age. Nat. Commun. 6:1–10. doi:10.1038/ncomms9706.

Poirier, M.G., and J.F. Marko. 2002. Mitotic chromosomes are chromatin networks without a mechanically contiguous protein scaffold. Proc. Natl. Acad. Sci. U. S. A. 99:15393–15397. doi:10.1073/pnas.232442599.

Pope, L.H., C. Xiong, and J.F. Marko. 2006. Proteolysis of Mitotic Chromosomes Induces Gradual and Anisotropic Decondensation Correlated with a Reduction of Elastic Modulus and Structural Sensitivity to Rarely Cutting Restriction Enzymes. Mol. Biol. Cell. 17:104. doi:10.1091/MBC.E05-04-0321.

Dos Santos, Á., A.W. Cook, R.E. Gough, M. Schilling, N.A. Olszok, I. Brown, L. Wang, J. Aaron, M.L. Martin-Fernandez, F. Rehfeldt, and C.P. Toseland. 2021. DNA damage alters nuclear mechanics through chromatin reorganization. Nucleic Acids Res. 49:340–353. doi:10.1093/nar/gkaa1202.

Sun, M., R. Biggs, J. Hornick, and J.F. Marko. 2018. Condensin controls mitotic chromosome stiffness and stability without forming a structurally contiguous scaffold. Chromosom. Res. 26:277–295. doi:10.1007/s10577-018-9584-1.

Thompson, S.L., and D.A. Compton. 2011. Chromosomes and cancer cells. Chromosom. Res. 19:433–444. doi:10.1007/s10577-010-9179-y.

Ward, A., J. Hopkins, M. Mckay, S. Murray, and P.W. Jordan. 2016. Genetic Interactions Between the Meiosis-Specific Cohesin Components, STAG3, REC8, and RAD21L. G3 (Bethesda). 6:1713–24. doi:10.1534/g3.116.029462.

Winship, A.L., J.M. Stringer, S.H. Liew, and K.J. Hutt. 2018. The importance of DNA repair for maintaining oocyte quality in response to anti-cancer treatments, environmental toxins and maternal ageing. Hum. Reprod. Update. 24:119–134. doi:10.1093/humupd/dmy002.

Xu, H., M.D. Beasley, W.D. Warren, G.T.J. van der Horst, and M.J. McKay. 2005. Absence of Mouse REC8 Cohesin Promotes Synapsis of Sister Chromatids in Meiosis. Dev. Cell. 8:949–961. doi:10.1016/j.devcel.2005.03.018.

Author response:

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

Reviewer #1:<br /> (1) I still think that the authors need to set the importance of the differences in aggregation in the context of toxicity arising from protein misfolding/aggregation. While the authors state the limitation in the response, and I agree that a single manuscript cannot complete a field of investigation I still think that this is an important point missing from this manuscript.

We thank the reviewer for the comments, we are working to address this issue and will elucidate in our future studies.

(2) I retain my reservations about the fluorescence intensity data shown for Rho123, DCF, Jc1, and MitoSox. The errors are much lower than what we typically achieve in biological experiments in our as well as our collaborator's lab. A glimpse at published literature would also support our statement. Specifically, RHO123 shows a large difference in errors between Figure 5 and Figure 5 Supplement 2. The point to note is that the absolute intensities do not vary between these figures, but the errors are the order of magnitude lower in the main figures. I, therefore, accept these figures in good faith without further interrogation.

We really value these comments from the reviewer and also do not want to cause any potential misleading interpretations of the data. We have therefore asked a more experienced author to redo all the experiments on the physiological indicators (Rho123, JC1 and MitoSox) that directly reflect mitochondrial function, and left out the DCF data. The new experimental data are in line with our previous results. We have clearly described these changes in the Results, Materials and Methods and Figure legends sections.

The new data from the redo experiments are: Rho123 fluorescence intensity data in Figure 5A, B and C; Figure 6B; JC1 staining in Figure 6E; JC1 staining in Figure 7A, B and D.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This paper introduces a new approach to modeling human behavioral responses using image-computable models. They create a model (VAM) that is a combination of a standard CNN coupled with a standard evidence accumulation model (EAM). The combined model is then trained directly on image-level data using human behavioral responses. This approach is original and can have wide applicability. However, many of the specific findings reported are less compelling.

Strengths:

(1) The manuscript presents an original approach to fitting an image-computable model to human behavioral data. This type of approach is sorely needed in the field.

(2) The analyses are very technically sophisticated.

(3) The behavioral data are large both in terms of sample size (N=75) and in terms of trials per subject.

Weaknesses:

Major

(1) The manuscript appears to suggest that it is the first to combine CNNs with evidence accumulation models (EAMs). However, this was done in a 2022 preprint

(https://www.biorxiv.org/content/10.1101/2022.08.23.505015v1) that introduced a network called RTNet. This preprint is cited here, but never really discussed. Further, the two unique features of the current approach discussed in lines 55-60 are both present to some extent in RTNet. Given the strong conceptual similarity in approach, it seems that a detailed discussion of similarities and differences (of which there are many) should feature in the Introduction.

Thanks for pointing this out—we agree that the novel contributions of our model (the VAM) with respect to prior related models (including RTNet) should be clarified, and have revised the Introduction accordingly. We include the following clarifications in the Introduction:

“The key feature of the VAM that distinguishes it from prior models is that the CNN and EAM parameters are jointly fitted to the RT, choice, and visual stimulus data from individual participants in a unified Bayesian framework. Thus, both the visual representations learned by the CNN and the EAM parameters are directly constrained by behavioral data. In contrast, prior models first optimize the CNN to perform the behavioral task, then separately fit a minimal set of high-level CNN parameters [RTNet, Rafiei et al., 2024] and/or the EAM parameters to behavioral data [Annis et al., 2021; Holmes et al., 2020; Trueblood et al., 2021]. As we will show, fitting the CNN with human data—rather than optimizing the model to perform a task—has significant consequences for the representations learned by the model.”

E.g. in the case of RTNet, the variability of the Bayesian CNN weight distribution, the decision threshold, and the magnitude of the noise added to the images are adjusted to match the average human accuracy (separately for each task condition). RTNet is an interesting and useful model that we believe has complementary strengths to our own work.

Since there are several other existing models in addition to the VAM and RTNet that use CNNs to generate RTs or RT proxies (by our count, at least six that we cite earlier in the Introduction), we felt it was inappropriate to preferentially include a detailed comparison of the VAM and RTNet beyond the passage quoted above.

(2) In the approach here, a given stimulus is always processed in the same way through the core CNN to produce activations v_k. These v_k's are then corrupted by Gaussian noise to produce drift rates d_k, which can differ from trial to trial even for the same stimulus. In other words, the assumption built into VAM appears to be that the drift rate variability stems entirely from post-sensory (decisional) noise. In contrast, the typical interpretation of EAMs is that the variability in drift rates is sensory. This is also the assumption built into RTNet where the core CNN produces noisy evidence. Can the authors comment on the plausibility of VAM's assumption that the noise is post-sensory?

In our view, the VAM is compatible with a model in which the drift rate variability for a given stimulus is due to sensory noise, since we do not specify the origin of the Gaussian noise added to the drift rates. As the reviewer notes, the CNN component of the VAM processes a given stimulus deterministically, yielding the mean drift rates. This does not preclude us from imagining an additional (unmodeled) sensory process that adds variability to the drift rates. The VAM simply represents this and other hypothetical sources of variability as additive Gaussian noise. We agree however that it is worthwhile to think about the origin of the drift rate variability, though it is not a focus of our work.

(3) Figure 2 plots how well VAM explains different behavioral features. It would be very useful if the authors could also fit simple EAMs to the data to clarify which of these features are explainable by EAMs only and which are not.

In our view, fitting simple EAMs to the data would not be especially informative and poses a number of challenges for the particular task we study (LIM) that are neatly avoided by using the VAM. In particular, as we show in Figure 2, the stimuli vary along several dimensions that all appear to influence behavior: horizontal position, vertical position, layout, target direction, and flanker direction. Since the VAM is stimulus-computable, fitting the VAM automatically discovers how all of these stimulus features influence behavior (via their effect on the drift rates outputted by the CNN). In contrast, fitting a simple EAM (e.g. the LBA model) necessitates choosing a particular parameterization that specifies the relationship between all of the stimulus features and the EAM model parameters. This raises a number of practical questions. For example, should we attempt to fit a separate EAM for each stimulus feature, or model all stimulus features simultaneously?

Moreover, while we could in principle navigate these issues and fit simple EAMs to the data, we do not intend to claim that simple EAMs fail to explain the relationship between stimulus features and behavior as well as the VAM. Rather, the key strength of the VAM relative to simple EAMs is that it includes a detailed and biologically plausible model of human vision. The majority of the paper capitalizes on this strength by showing how behavioral effects of interest (namely congruency effects) can be explained in terms of the VAM’s visual representations.

(4) VAM is tested in two different ways behaviorally. First, it is tested to what extent it captures individual differences (Figure 2B-E). Second, it is tested to what extent it captures average subject data (Figure 2F-J). It wasn't clear to me why for some metrics only individual differences are examined and for other metrics only average human data is examined. I think that it will be much more informative if separate figures examine average human data and individual difference data. I think that it's especially important to clarify whether VAM can capture individual differences for the quantities plotted in Figures 2F-J.

We would like to clarify that Fig. 2J in fact already shows how well the VAM captures individual differences for the average subject data shown in Fig. 2H (stimulus layout) and Fig. 2I (stimulus position). For a given participant and stimulus feature, we calculated the Pearson's r between model/participant mean RTs across each stimulus feature value. Fig. 2J shows the distribution of these Pearson’s r values across all participants for stimulus layout and horizontal/vertical position.

Fig. 2G also already shows how well the VAM captures individual differences in behavior. Specifically, this panel shows individual differences in mean RT attributable to differences in age. For Fig. 2F, which shows how the model drift rates differ on congruent vs. incongruent trials, there is no sensible way to compare the models to the participants at any level of analysis (since the participants do not have drift rates). 

(5) The authors look inside VAM and perform many exploratory analyses. I found many of these difficult to follow since there was little guidance about why each analysis was conducted. This also made it difficult to assess the likelihood that any given result is robust and replicable. More importantly, it was unclear which results are hypothesized to depend on the VAM architecture and training, and which results would be expected in performance-optimized CNNs. The authors train and examine performance-optimized CNNs later, but it would be useful to compare those results to the VAM results immediately when each VAM result is first introduced.

Thanks for pointing this out—we apologize for any confusion caused by our presentation of the CNN analyses. We have added in additional motivating statements, methodological clarifications, and relevant references to our Results, particularly for Figure 3 in which we first introduce the analyses of the CNN representations/activity. In general, each analysis is prefaced by a guiding question or specific rationale, e.g. “How do the models' visual representations enable target selectivity for stimuli that vary along several irrelevant dimensions?” We also provide numerous references in which these analysis techniques have been used to address similar questions in CNNs or the primate visual cortex.

We chose to maintain the current organization of our results in which the comparison between the VAM and the task-optimized models are presented in a separate figure. We felt that including analyses of both the VAM and task-optimized models in the initial analyses of the CNN representations would be overwhelming for many readers. As the reviewer acknowledges, some readers may already find these results challenging to follow. 

(6) The authors don't examine how the task-optimized models would produce RTs. They say in lines 371-2 that they "could not examine the RT congruency effect since the task-optimized models do not generate RTs." CNNs alone don't generate RTs, but RTs can easily be generated from them using the same EAM add-on that is part of VAM. Given that the CNNs are already trained, I can't see a reason why the authors can't train EAMs on top of the already trained CNNs and generate RTs, so these can provide a better comparison to VAM.

We appreciate this suggestion, but we judge the suggestion to “train EAMs on top of the already trained CNNs and generate RTs” to be a significant expansion of the scope of the paper with multiple possible roads forward. In particular, one must specify how the outputs of the task-optimized CNN (logits for each possible response) relate to drift rates, and there is no widely-accepted or standard way to do this. Previously proposed methods include transforming representation distances in the last layer to drift rates (https://doi.org/10.1037/xlm0000968), fitting additional subject-specific parameters that map the logits to drift rates

(https://doi.org/10.1007/s42113-019-00042-1), or using the softmax-scored model outputs as drift rates directly (https://doi.org/10.1038/s41562-024-01914-8), though in the latter case the RTs are not on the same scale as human data. In our view, evaluating these different methods is beyond the scope of this paper. An advantage of the VAM is that one does not have to fit two separate models (a CNN and a EAM) to generate RTs.

Nonetheless, we agree that it would be informative to examine something like RTs in the task-optimized models. Our revised Results section now includes an analysis of the confidence of the task-optimized models’ decisions, which we use a proxy for RTs:   

“Since the task-optimized models do not generate RTs, it is not possible to directly measure RT congruency effects in these models without making additional assumptions about how the CNN's classification decisions relate to RTs. However, as a coarse proxy for RT, we can examine the confidence of the CNN's decisions, defined as the softmax-scored logit (probability) of the most probable direction in the final CNN layer. This choice of RT proxy is motivated by some prior studies that have combined CNNs with EAMs [Annis et al., 2021; Holmes et al., 2020; Trueblood et al., 2021]. These studies explicitly or implicitly derive a measure of decision confidence from the activity of the last CNN layer. The confidence measure is then mapped to the EAM drift rates, such that greater decision confidence generally corresponds to higher drift rates (and therefore shorter RTs).

We calculated the average confidence of each task-optimized CNN separately for congruent vs. incongruent trials. On average, the task-optimized models showed higher confidence on congruent vs. incongruent trials (W = 21.0, p < 1e-3, Wilcoxon signed-rank test; Cohen's d = 0.99; n = 75 models). These analyses therefore provide some evidence that task-optimized CNNs have the capacity to exhibit congruency effects, though an explicit comparison of the magnitude of these effects with human data requires additional modeling assumptions (e.g., fitting a separate EAM).”

(7) The Discussion felt very long and mostly a summary of the Results. I also couldn't shake the feeling that it had many just-so stories related to the variety of findings reported. I think that the section should be condensed and the authors should be clearer about which explanations are speculations and which are air-tight arguments based on the data.

We have shortened the Discussion modestly and we have added in some clarifying language to help clarify which arguments are more speculative vs. directly supported by our data.

Specifically, we added in the phrase “we speculate that…” for two suggestions in the Discussion (paragraphs 3 and 5), and we ensured that any other more speculative suggestions contain such clarifying language. We have also added in subheadings in the Discussion to help readers navigate this section. 

(8) In one of the control analyses, the authors train different VAMs on each RT quantile. I don't understand how it can be claimed that this approach can serve as a model of an individual's sensory processing. Which of the 5 sets of weights (5 VAMs) captures a given subject's visual processing? Are the authors saying that the visual system of a given subject changes based on the expected RT for a stimulus? I feel like I'm missing something about how the authors think about these results.

We agree that these particular analyses may cause confusion and have removed them from our revised manuscript.

Reviewer #2 (Public Review):

In an image-computable model of speeded decision-making, the authors introduce and fit a combined CCN-EAM (a 'VAM') to flanker-task-like data. They show that the VAM can fit mean RTs and accuracies as well as the congruency effect that is present in the data, and subsequently analyze the VAM in terms of where in the network congruency effects arise.

Overall, combining DNNs and EAMs appears to be a promising avenue to seriously model the visual system in decision-making tasks compared to the current practice in EAMs. Some variants have been proposed or used before (e.g., doi.org/10.1016/j.neuroimage.2017.12.078 , doi.org/10.1007/s42113-019-00042-1), but always in the context of using task-trained models, rather than models trained on behavioral data. However, I was surprised to read that the authors developed their model in the context of a conflict task, rather than a simpler perceptual decision-making task. Conflict effects in human behavior are particularly complex, and thereby, the authors set a high goal for themselves in terms of the to-be-explained human behavior. Unfortunately, the proposed VAM does not appear to provide a great account of conflict effects that are considered fundamental features of human behavior, like the shape of response time distributions, and specifically, delta plots (doi.org/10.1037/0096-1523.20.4.731). The authors argue that it is beyond the scope of the presented paper to analyze delta plots, but as these are central to studies of human conflict behavior, models that aim to explain conflict behavior will need to be able to fit and explain delta plots.

Theories on conflict often suggest that negative/positive-trending delta plots arise through the relative timing of response activation related to relevant and irrelevant information.

Accumulation for relevant and irrelevant information would, as a result, either start at different points in time or the rates vary over time. The current VAM, as a feedforward neural network model, does not appear to be able to capture such effects, and perhaps fundamentally not so: accumulation for each choice option is forced to start at the same time, and rates are a static output of the CNN.

The proposed solution of fitting five separate VAMs (one for each of five RT quantiles) is not satisfactory: it does not explain how delta plots result from the model, for the same reason that fitting five evidence accumulation models (one per RT quantile) does not explain how response time distributions arise. If, for example, one would want to make a prediction about someone's response time and choice based on a given stimulus, one would first have to decide which of the five VAMs to use, which is circular. But more importantly, this way of fitting multiple models does not explain the latent mechanism that underlies the shape of the delta plots.

As such, the extensive analyses on the VAM layers and the resulting conclusions that conflict effects arise due to changing representations across layers (e.g., "the selection of task-relevant information occurs through the orthogonalization of relevant and irrelevant representations") - while inspiring, they remain hard to weigh, as they are contingent on the assumption that the VAM can capture human behavior in the conflict task, which it struggles with. That said, the promise of combining CNNs and EAMs is clearly there. A way forward could be to either adjust the proposed model so that it can explain delta plots, which would potentially require temporal dynamics and time-varying evidence accumulation rates, or perhaps to start simpler and combine CCNs-EAMs that are able to fit more standard perceptual decision-making tasks without conflict effects.

We thank the reviewer for their thoughtful comments on our work. However, we note that the

VAM does in fact capture the positive-trending RT delta plot observed in the participant data (Fig. S4A), though the intercepts for models/participants differ somewhat. On the other hand, the conditional accuracy functions (Fig. S4B) reveal a more pronounced difference between model and participant behavior. As the reviewer points out, capturing these effects is likely to require a model that can produce time-varying drift rates, whereas our model produces a fixed drift rate for a given stimulus. We also agree that fitting a separate VAM to each RT quantile is not a satisfactory means of addressing this limitation and have removed these analyses from our revised manuscript.

However, while we agree that accurately capturing these dynamic effects is a laudable goal, it is in our view also worthwhile to consider explanations for the mean behavioral effect (i.e. the accuracy congruency effect), which can occur independently of any consideration of dynamics. One of our main findings is that across-model variability in accuracy congruency effects is better attributed to variation in representation geometry (target/flanker subspace alignment) vs.

variation in the degree of flanker suppression. This finding does not require any consideration of dynamics to be valid at the level of explanation we pursue (across-user variability in congruency effects), but also does not preclude additional dynamic processes that could give rise to more specific error patterns. Our revised discussion now includes a section where we summarize and elaborate on these ideas:

“It is not difficult to imagine how the orthogonalization mechanism described above, which explains variability in accuracy congruency effects across individuals, could act in concert with other dynamic processes that explain variability in congruency effects within individuals (e.g., as a function of RT). In general, any process that dynamically gates the influence of irrelevant sensory information on behavioral outputs could accomplish this, for example ramping inhibition of incorrect response activation [https://doi.org/10.3389/fnhum.2010.00222], a shrinking attention spotlight [https://doi.org/10.1016/j.cogpsych.2011.08.001], or dynamics in neural population-level geometry [https://doi.org/10.1038/nn.3643]. To pursue these ideas, future work may aim to incorporate dynamics into the visual component and decision component of the VAM with recurrent CNNs [https://doi.org/10.48550/arXiv.1807.00053, https://doi.org/10.48550/arXiv.2306.11582] and the task-DyVA model [https://doi.org/10.1038/s41562-022-01510-8], respectively.”

Reviewer #3 (Public Review):

Summary:

In this article, the authors combine a well-established choice-response time (RT) model (the Linear Ballistic Accumulator) with a CNN model of visual processing to model image-based decisions (referred to as the Visual Accumulator Model - VAM). While this is not the first effort to combine these modeling frameworks, it uses this combination of approaches uniquely.

Specifically, the authors attempt to better understand the structure of human information representations by fitting this model to behavioral (choice-RT) data from a classic flanker task. This objective is made possible by using a very large (by psychological modeling standards) industry data set to jointly fit both components of this VAM model to individual-level data. Using this approach, they illustrate (among other results) (1) how the interaction between target and flanker representations influence the presence and strength of congruency effects, (2) how the structure of representations changes (distributed versus more localized) with depth in the CNN model component, and (3) how different model training paradigms change the nature of information representations. This work contributes to the ML literature by demonstrating the value of training models with richer behavioral data. It also contributes to cognitive science by demonstrating how ML approaches can be integrated into cognitive modeling. Finally, it contributes to the literature on conflict modeling by illustrating how information representations may lead to some of the classic effects observed in this area of research.

Strengths:

(1) The data set used for this analysis is unique and is made publicly available as part of this article. Specifically, they have access to data for 75 participants with >25,000 trials per participant. This scale of data/individual is unusual and is the foundation on which this research rests.

(2) This is the first time, to my knowledge, that a model combining a CNN with a choice-RT model has been jointly fit to choice-RT data at the level of individual people. This type of model combination has been used before but in a more restricted context. This joint fitting, and in particular, learning a CNN through the choice-RT modeling framework, allows the authors to probe the structure of human information representations learned directly from behavioral data.

(3) The analysis approaches used in this article are state-of-the-art. The training of these models is straightforward given the data available. The interesting part of this article (opinion of course) is the way in which they probe what CNN has learned once trained. I find their analysis of how distractor and target information interfere with each other particularly compelling as well as their demonstration that training on behavioral data changes the structure of information representations when compared to training models on standard task-optimized data.

Weaknesses:

(1) Just as the data in this article is a major strength, it is also a weakness. This type of modeling would be difficult, if not impossible to do with standard laboratory data. I don't know what the data floor would be, but collecting tens of thousands of decisions for a single person is impractical in most contexts. Thus this type of work may live in the realm of industry. I do want to re-iterate that the data for this study was made publicly available though!

We suspect (but have not systematically tested) that the VAMs can be fitted with substantially less data. We use data augmentation techniques (various randomized image transformations) during training to improve the generalization capabilities of the VAMs, and these methods are likely to be particularly important when training on smaller datasets. One could consider increasing the amount of image data augmentation when working with smaller datasets, or pursuing other forms of data augmentation like resampling from estimated RT distributions (see https://doi.org/10.1038/s41562-022-01510-8 for an example of this). In general, we don’t think that prospective users of our approach should be discouraged if they have only a few hundred trials per subject (or less) - it’s worth trying!

(2) While this article uses choice-RT data it doesn't fully leverage the richness of the RT data itself. As the authors point out, this modeling framework, the LBA component in particular, does not account for some of the more nuanced but well-established RT effects in this data. This is not a big concern given the already nice contributions of this article and it leads to an opportunity for ongoing investigation.

We agree that fully capturing the more nuanced behavioral effects you mention (e.g. RT delta plots and conditional accuracy functions) is a worthwhile goal for future research—see our response to Reviewer #2 for a more detailed discussion. ----------

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) The phrase in the Abstract "convolutional neural network models of visual processing and traditional EAMs are jointly fitted" made me initially believe that the two models were fitted independently. You may want to re-word to clarify.

We think that the phrase “jointly fitted” already makes it clear that both the CNN and EAM parameters are estimated simultaneously, in agreement with how this term is usually used. But we have nonetheless appended some additional clarifying language to that sentence (“in a unified Bayesian framework”).

(2) Lines 27-28: EAMs "are the most successful and widely-used computational models of decision-making." This is only true for the specific type of decision-making examined here, namely joint modeling of choice and response times. Signal detection theory is arguably more widely-used when response times are not modeled.

Thanks for pointing this out - we have revised the referenced sentence accordingly.

(3) Could the authors clarify what is plotted in Figure 2F?

Fig. 2F shows the drift rates for the target, flanker, and “other” (non-target/non-flanker) accumulators averaged over trials and models for congruent vs. incongruent trials. In case this was a source of confusion, we do not show the value of the flanker drift rates on congruent trials because the flanker and target accumulators are identical (i.e. the flanker/congruent drift rates are equivalent to the target/congruent drift rates).

(4) Lines 214-7: "The observation that single-unit information for target direction decreased between the fourth and final convolutional layers while population-level decoding remained high is especially noteworthy in that it implies a transition from representing target direction with specialized "target neurons" to a more distributed, ensemble-level code." Can the authors clarify why this is the only reasonable explanation for these results? It seems like many other explanations could be construed.

We have added additional clarification to this section and now use more tentative language:

“The observation that single-unit information for target direction decreased between the fourth and final convolutional layers indicates that the units become progressively less selective for particular target directions. Since population-level decoding remained high in these layers, this suggests a transition from representing target direction with specialized "target neurons" to a more distributed, ensemble-level code.”

(5) Lines 372-376: "Thus, simply training the model to perform the task is not sufficient to reproduce a behavioral phenomenon widely-observed in conflict tasks. This challenges a core (but often implicit) assumption of the task-optimized training paradigm, namely that to do a task well, a training model will result in model representations that are similar to those employed by humans." While I agree with the general sentiment, I feel that its application here is strange. Unless I'm missing something, in the context of the preceding sentence, the authors seem to be saying that researchers in the field expect that CNNs can produce a behavioral phenomenon (RTs) that is completely outside of their design and training. I don't think that anyone actually expects that.

We moved the discussion/analyses of RTs to the next paragraph. It should now be clear that this statement refers specifically to the absence of an accuracy congruency effect in the task-optimized models.

(6) Lines 387-389: "As a result, the VAMs may learn richer representations of the stimuli, since a variety of stimulus features-layout, stimulus position, flanker direction-influence behavior (Figure 2)." That is certainly true of tasks like this one where an optimal model would only focus on a tiny part of the image, whereas humans are distracted by many features. I'm not sure that this distractibility is the same as "richer representations". When CNNs classify images based on the background, would the authors claim that they have richer representations than humans?

We agree that “richer” may not be the best way to characterize these representations, and have changed it to “more complex”.

(7) Is it possible that drift rate d_k for each response happens to be negative on a given trial? If so, how is the decision given on such trials (since presumably none of the accumulators will ever reach the boundary)?

It is indeed possible for all of the drift rates to be negative, though we found that this occurred for a vanishingly small number of trials (mean ± s.e.m. percent trials/model: 0.080 ± 0.011%, n = 75 models), as reported in the Methods. These trials were excluded from analyses.

(8)  Can the authors comment on how they chose the CNN architecture and whether they expect that different architectures will produce similar results?

Before establishing the seven-layer CNN architecture used throughout the paper, we conducted some preliminary experiments using other architectures that differed primarily in the number of CNN layers. We found that models with significantly fewer than seven layers typically failed to reach human-level accuracy on the task while larger models achieved human-level accuracy but (unsurprisingly) took longer to train.

Reviewer #3 (Recommendations For The Authors):

- In the introduction to this paper (particularly the paragraph beginning in line 33), the authors note that EAMs have typically been used in simplified settings and that they do not provide a means to account for how people extract information from naturalistic stimuli. While I agree with this, the idea of connecting CNNs of visual processing with EAMs for a joint modeling framework has been done. I recommend looking at and referencing these two articles as well as adjusting the tenor of this part of an introduction to better reflect the current state of the literature. For full disclosure, I am one of the authors on these articles. https://link.springer.com/article/10.1007/s42113-019-00042-1 https://www.sciencedirect.com/science/article/abs/pii/S0010027721001323

We agree—thanks for pointing this out. The revised Introduction now discusses prior related models in more detail (including those referenced above) and better clarifies the novel contributions of our model. We specifically highlight that a novel contribution of the VAM is that “the CNN and EAM parameters are jointly fitted to the RT, choice, and visual stimulus data from individual participants in a unified Bayesian framework.”

- The statement in lines 56-58 implies that this is the first article to glue CNNs together with EAMs. I would edit this accordingly based on the prior comment here and references provided. I will note that the second feature of the approach in this paper is still novel and really nice, namely the fact that the CNN and the EAM are jointly fitted. In the aforementioned references, the CNN is trained on the image set, and individual level Bayesian estimation was only applied to the EAM. Thus, it may be useful to highlight the joint estimation aspect of this investigation as well as how the uniqueness of the data available makes it possible.

Agreed—see above.

- Figure 3c and associated text. I understand the MI analysis you are performing here, however it is difficult to interpret as it stands. In the figure, what does a MI of 0.1 mean?? Can you give some context to that scale? I do find the interpretation of the hunchback shape in lines 210-222 to be somewhat of a stretch. The discussion that precedes (lines 199-209) this is clear and convincing. Can this discussion be strengthened more? And more interpretability of Figure 3c would be helpful; entropic scales can be hard to interpret without some context or scale associated.

The MI analyses in Fig. 3C (and also Figs. 4C and 6E) show normalized MI, in which the raw MI has been divided by the entropy of the stimulus feature distribution. This normalization facilitates comparing the MI for different stimulus features, which is relevant for Figs. 4C and 6E. The normalized MI has a possible range of [0, 1], where 1 indicates perfect correlation between the two variables and 0 indicates complete independence. We now note in the legend of these figures that the possible normalized MI range is [0, 1], which should help with interpreting these values. Our revised results section for Fig. 3C now also includes some additional remarks on our interpretation of the hunchback shape of the MI.

- Lines 244-248 and the analyses in Figure 3 suggest a change in the behavior of the CNN around layer 4. This is just a musing, but what would happen if you just used a 4 layer CNN, or even a 3 layer? This is not just a methods question. Your analysis suggests a transition from localized to distributed information representation. Right now, the EAM only sees the output of the distributed representation. What if it saw the results the more local representations from early layers? Of course, a shallower network may just form the distributed representations earlier, but it would interesting if there were a way to tease out not just the presence of distributed vs local representations, but the utility of those to the EAM.

Thanks for this interesting suggestion. We did do some preliminary experiments in models with fewer layers, though we only examined the outputs of these models and did not assess their representations. We found that models with 3–5 layers generally failed to achieve human-level accuracy on the task. In principle, one could relate this observation to the representations of these models as a means of assessing the relative utility of distributed/local representations. However, there are confounding factors that one would ideally control for in order to compare models with different numbers of layers in this fashion (namely, the number of parameters).

- Section Line 359 (Task optimized models) - It would be helpful to clarify here what these task-optimized models are being trained to do. As I understand it, they are being trained to directly predict the target direction. But are you asking them to learn to predict the true target direction? Or are you training them to predict what each individual responds? I think it is the second (since you have 75 of these), but it's not clear. I looked at the methods and still couldn't get a clear description of this. Also, are you just stripping the LBA off of the end of the CNN and then essentially putting a softmax in its place? If so, it would be helpful to say so.

The task-optimized models were actually trained to output the true target direction in each stimulus, rather than trained to match the decisions of the human participants. We trained 75 such models since we wanted to use exactly the same stimuli as were used to train each VAM. The task-optimized CNNs were identical to those used in the VAMs, except that the outputs of the last layer were converted to softmax-scored probabilities for each direction rather than drift rates. The Results and Methods section now included additional commentary that clarifies these points.

- Line 373-376: This statement is pretty well established at this point in the similarity judgement literature. I recommend looking at and referencing https://onlinelibrary.wiley.com/doi/full/10.1111/cogs.13226 https://www.nature.com/articles/s41562-020-00951-3 https://link.springer.com/article/10.1007/s42113-020-00073-z

Thanks for pointing this out. For reference, the statement in question is “Thus, simply training the model to perform the task is not sufficient to reproduce a behavioral phenomenon widely-observed in conflict tasks. This challenges a core (but often implicit) assumption of the task-optimized training paradigm, namely that training a model to do a task well will result in model representations that are similar to those employed by humans.”

We agree that the first and third reference you mention are relevant, and we now cite them along with some other relevant work. In our view, the second reference you mention is not particularly relevant (that paper introduces a new computational model for similarity judgements that is fit to human data, but does not comment on training models to perform tasks vs. fitting to human data).

- Line 387-388: "VAMs may learn richer representations". This is a bit of a philosophical point, but I'll go ahead and mention it. The standard VAM does not necessarily learn "richer" feature representations. Rather, you are asking the VAM and task-optimized models to do different things. As a result, they learn different representations. "Better" or "richer" is in the eye of the beholder. In one view, you could view the VAM performance as sub-par since it exhibits strange artifacts (congruency effects) and the expansion of dimensionality in the VAM representations is merely a side-effect of poor performance. I'm not advocating this view, just playing devils advocate and suggesting a more nuanced discussion of the difference between the VAM and task-optimized models.

We agree—this is a great point. We have changed this statement to read “the VAMs may learn more complex [rather than richer] representations of the stimuli”.

- Lines 567-570: Here you discuss how the LBA backend of the VAM can't account for shrinking spotlight-like RT effects but that fitting models to different RT quantiles helps overcome this. I find this to be one of the weakest points of the paper (the whole process of fitting RT quantiles separately to begin with). This is just a limitation of the RT component of the model. This is a great paper but this is just a limitation inherent in the model. I don't see a need to qualify this limitation and think it would be better to just point out that this is a limitation of the LBA itself (be more clear that it is the LBA that is the limiting factor here) and that this leaves room for future research. From your last sentence of this paragraph, I agree that recurrent CNNs would be interesting. I will note that RNN choice-RT models are out there (though not with CNNs as part of the model).

We agree and have revised this section of the Discussion accordingly (see our response to Reviewer #2 for more detail). We also removed the analyses of models trained on separate RT quantiles.

Author response:

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

eLife Assessment

The study presents a potentially valuable approach to genetically modify cells to produce extracellular matrices with altered compositions, termed cell-laid, engineered extracellular matrices (eECM). The evidence supporting the authors' conclusions regarding the utility of eECM for endogenous repair is solid, although there are some disagreements on the chondrogenicity of lyophilized constructs which was viewed as lacking robust evidence for endochondral ossification.

We thank the reviewers for the assessment of our work. We however strongly contest the lack of evidence for chondrogenicity and endochondral ossification. This is robustly demonstrated and a clear strength of our study.

Public Reviews:

Reviewer #1 (Public review):

Summary:

The authors aimed to modify the characteristics of the extracellular matrix (ECM) produced by immortalized mesenchymal stem cells (MSCs) by employing the CRISPR/Cas9 system to knock out specific genes. Initially, they established VEGF-KO cell lines, demonstrating that these cells retained chondrogenic and angiogenic properties. Additionally, lyophilized carriage tissues produced by these cells exhibited retained osteogenic properties.

Subsequently, the authors established RUNX2-KO cell lines, which exhibited reduced COLX expression during chondrogenic differentiation and notably diminished osteogenic properties in vitro. Transplantation of lyophilized carriage tissues produced by RUNX2-KO cell lines into osteochondral defects in rat knee joints resulted in the regeneration of articular cartilage tissues as well as bone tissues, a phenomenon not observed with tissues derived from parental cells. This suggests that gene-edited MSCs represent a valuable cell source for producing ECM with enhanced quality.

Strengths:

The enhanced cartilage regeneration observed with ECM derived from RUNX2-KO cells supports the authors' strategy of creating gene-edited MSCs capable of producing ECM with superior quality. Immortalized cell lines offer a limitless source of off-the-shelf material for tissue regeneration.

Weaknesses:

Most of the data align with anticipated outcomes, offering limited novelty to advance scientific understanding. Methodologically, the chondrogenic differentiation properties of immortalized MSCs appeared deficient, evidenced by Safranin-O staining of 3D tissues and histological findings lacking robust evidence for endochondral differentiation. This presents a critical limitation, particularly as authors propose the implantation of cartilage tissues for in vivo experiments. Instead, the bulk of data stemmed from type I collagen scaffold with factors produced by MSCs stimulated by TGFβ.

We thank the reviewer for the thorough evaluation. We appreciate the highlighted novelty but overall disagree with key points from the provided assessment. The most important one being non the contested in vitro cartilage and endochondral ossification by engineered ECMs, for which we have provided compelling evidence. Of note, the reviewer points the “osteogenic” properties of our tissues; the wording is incorrect since cells are absent from the final grafts. Here, the term ”osteoinductivity” should be employed, in line with the model of ectopic ossification used to demonstrate de novo bone formation.

In the revised version, the authors presented Safranin-O staining results of pellets prior to lyophilization. The inset of figures showing entire pellets revealed that Safranin-O-positive areas were limited, suggesting that cells in the negative regions had not differentiated into chondrocytes. In Figure 3F, DAPI staining showed devitalized cells in the outer layer but was negative in the central part, indicating the absence of cells in these areas and incomplete differentiation induction.

We strongly disagree with the reviewer on the lack of demonstrated chondrogenicity. We have provided evidence of Safranin-O positivity, GAGs quantification, as well as collagen type 2 and collagen type X stainings (also quantified). Frankly, those are gold standard assays in the field and we do not understand the reviewer point of view. We however agree that our grafts are not entirely composed of cartilage matrix. There are areas where cartilage is absent, in particular in the core of the tissues. This is expected from in vitro engineered cartilage pellets even from primary BM-MSCs donors. By selecting primary donors it is possible to obtain a superior cartilage formation. Our MSOD-B cells remain to-the-best-of-our -knowledge, the only human line capable of in vitro chondrogenesis, even if considered moderate.

We agree with the absence of cells in the core area of our tissues, as correctly pointed out by the reviewer. This has been reported in other studies whereby the lack of media diffusion can lead to necrotic core formation.

The rationale for establishing VEGF-KO cell lines remains unclear, and the authors' explanation in the revised manuscript is still equivocal. While they mention that VEGF is a late marker for endochondral ossification, the data in Figures 1D and 1E clearly show that VEGF-KO affects the early phase of endochondral ossification.

We feel that the rationale for a VEGF-KO is sufficiently conveyed. In our study, VEGF-KO affects GAGs content in the tissue, but not the efficiency of ossification.

Insufficient depth was given to elucidate the disparity in osteogenic properties between those observed in ectopic bone formation and those observed in transplantation into osteochondral defects.

We here agree with the reviewer on the limited depth of our osteochondral assessment. However, this was performed as a proof-of-concept and we clearly conveyed both limitations and need of a follow-up study to demonstrate the repair efficacy of our tissue in such defect context.

In the ectopic bone formation study, most of the collagenous matrix observed at 2 weeks was resorbed by 6 weeks, with only a small amount contributing to bone formation in MSOD-B cells (Figs. 2I and 4C). This finding does not align with the micro-CT data presented in Figures 2H and 4B. For the micro-CT experiments, it would be more appropriate to use a standard window for bone and present the data accordingly.

Stainings report the deposition of collagens and may be misleading as not only indicating frank bone formation. This is the reason why we provided microCT data, offering a quantitative assessment of the full grafts and more reliably evaluating mineralized/bone tissue. We feel that our results matched our conclusions.

While the regeneration of articular cartilage in RUNX2-KO ECM presents intriguing results, the study lacked an exploration into underlying mechanisms, such as histological analyses at earlier time points.

We do agree with the reviewer regarding this limitation. In addition to mechanisms and early timepoints, we are also interested in longer in vivo evaluation. This represents a significant amount of work which is beyond the scope of our present manuscript.

Reviewer #3 (Public review):

Summary:

In this study, the authors have started off using an immortalized human cell line and then gene edited it to decrease the levels of VEGF1 (in order to influence vascularization), and the levels of Runx2 (to decrease osteogenesis). They first transplanted these cells with a collagen scaffold. The modified cells showed a decrease in vascularization when VEGF1 was decreased, and suggested an increase in cartilage formation.

In another study, matrix generated by these cells subsequently remodeled into a bone marrow organ. When RUNX2 was decreased, the cells did not mineralize in vitro, and their matrices expressed types I and II collagen but not type X collagen in vitro, in comparison with unedited cells. In vivo, the author claims that remodeling of the matrices into bone was somewhat inhibited. Lastly, they utilized matrices generated by RUNX2-edited cells to regenerate chondro-osteal defects. They suggest that the edited cells regenerated cartilage in comparison with unedited cells.

Strengths:

- The notion that inducing changes in the ECM by genetically editing the cells is a novel one, as it has long been thought that ECM composition influences cell activity.

- If successful, it may be possible to make off the shelf ECMS to carry out different types of tissue repair.

Weaknesses:

- The authors have not demonstrated robust cartilage formation (quantitation would be useful).

- Measuring total GAG content does not prove the presence of cartilage

- There are numerous overstatements about forming and implanting cartilage.

- Although it is implied, RUNX2 deletion did not improve cartilage formation by the modified cells.

- In the control line, MSOD-B there were variability in the amount of safranin O positive material in various histological panels in the figures.; more quantitation is needed.

- In the in vivo articular defect experiments, an untreated injured joint is needed as a negative control.

- Statements about bone generation are often not reflective of the microCT data presented.<br /> - The discussion over-interprets the results.

We thank the reviewer for the further assessment of our work. We respectfully disagree with most of the provided statements. The chondrogenicity of our graft is robustly demonstrated using multiple readouts, including quantitative ones. Beyond GAGs, we provided clear Safranin-O stainings, as well as collagen type 2 and X indicating presence of hypertrophic cartilage matrix. Those are the gold standards in the field and we thus do not understand the reviewer scepticism. We do agree that our grafts are fully composed of cartilage matrix, with areas (in the core) deprived of cartilage. This does not impact the core findings of our study and its conclusions, and we strongly feel our statements about forming in vitro cartilage fully stand.

We do not claim in the manuscript an increased cartilage formation following RUNX2 deletion. We report in vitro an impaired hypertrophy (collagen type X) and maintenance of collagen type 2 and GAGs content.

We are confident on our data regarding de novo bone formation bi priming endochondral ossification, confirmed both by stainings and microCT. We feel that our claims are well-supported.

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

Public Reviews: 

Reviewer #1 (Public Review): 

Summary: 

The authors aimed to modify the characteristics of the extracellular matrix (ECM) produced by immortalized mesenchymal stem cells (MSCs) by employing the CRISPR/Cas9 system to knock out specific genes. Initially, they established VEGF-KO cell lines, demonstrating that these cells retained chondrogenic and angiogenic properties. Additionally, lyophilized carriage tissues produced by these cells exhibited retained osteogenic properties. 

Subsequently, the authors established RUNX2-KO cell lines, which exhibited reduced COLX expression during chondrogenic differentiation and notably diminished osteogenic properties in vitro. Transplantation of lyophilized carriage tissues produced by RUNX2-KO cell lines into osteochondral defects in rat knee joints resulted in the regeneration of articular cartilage tissues as well as bone tissues, a phenomenon not observed with tissues derived from parental cells. This suggests that gene-edited MSCs represent a valuable cell source for producing ECM with enhanced quality. 

Strengths: 

The enhanced cartilage regeneration observed with ECM derived from RUNX2-KO cells supports the authors' strategy of creating gene-edited MSCs capable of producing ECM with superior quality. Immortalized cell lines offer a limitless source of off-the-shelf material for tissue regeneration. 

We thank the reviewer for the interest in our work. We however want to clarify that the present manuscript does not report the generation of ECM with “superior quality”, but rather of modulated composition and thus function.  

Weaknesses: 

Most data align with anticipated outcomes, offering limited novelty to advance scientific understanding. Methodologically, the chondrogenic differentiation properties of immortalized MSCs appeared deficient, evidenced by Safranin-O staining of 3D tissues and histological findings lacking robust evidence for endochondral differentiation. This presents a critical limitation, particularly as authors propose the implantation of cartilage tissues for in vivo experiments. Instead, the bulk of data stemmed from type I collagen scaffold with factors produced by MSCs stimulated by TGFβ. 

The chondrogenic differentiation of our MSOD-B line and their capacity of undergoing endochondral ossification has been robustly demonstrated in previous studies (Pigeot et al., Advanced Materials 2021 and Grigoryan et al., Science Translational Medicine 2022). In the present manuscript, we thus compare the chondrogenic capacity of newly established VEGF-KO and RUNX-KO lines to those of MSOD-B cells. We demonstrate by qualitative (Safranin-O staining, Collagen type 2 and Collagen type X immuno-stainings) and quantitative (glycosaminoglycans assay) assays that the generated tissues consist in cartilage grafts of similar quality than the MSOD-B counterpart. Of note, the safranin-O stainings were performed on lyophilized tissues, which can alter the staining quality/intensity. We now provide additional stainings of generated tissues pre-lyophilization. This is implemented in Figure 1D, Figure 3D.

The rationale behind establishing VEGF-KO cell lines remains unclear. What specific outcomes did the authors anticipate from this modification? 

VEGF is a known master regulator of angiogenesis and a key mediator of endochondral ossification. It has also been extensively used in bone tissue engineering studies as a supplemented factor – primarily in the form of VEGFα – to increase the vascularization and thus outcome of bone formation of engineered grafts (https://www.nature.com/articles/s42003-020-01606-9, https://www.sciencedirect.com/science/article/pii/S8756328216301752). In our study, it was thus identified as a natural candidate to demonstrate the possibility to generate VEGF-KO cartilage and subsequently assess the functional impact on both the angiogenic and osteogenic potential of resulting cartilage tissue. This is now clarified in the manuscript (page 3, paragraph 4).

Insufficient depth was given to elucidate the disparity in osteogenic properties between those observed in ectopic bone formation and those observed in transplantation into osteochondral defects. While the regeneration of articular cartilage in RUNX2-KO ECM presents intriguing results, the study lacked an exploration into underlying mechanisms, such as histological analyses at earlier time points. 

Using RUNX2-KO ECM, we aimed at demonstrating the impact on cartilage remodeling and bone formation. This was performed ectopically but also in the rat osteochondral defect as a regenerative set-up of higher clinical relevance. We agree with the reviewer that additional experimental groups and time-points (not only earlier but also longer ones) would offer a better mechanistic understanding of the ECM contribution to the joint repair. However, as stated in our manuscript this is a proof-of-concept study that successfully demonstrated the influence of the cartilage ECM modification on the in vivo skeletal regeneration. A follow-up study would need to be performed to complement existing evidence and strengthen the relevance of our approach for cartilage repair. This is now further emphasized in the discussion (page 11, paragraph 3).  

Reviewer #2 (Public Review): 

The manuscript submitted by Sujeethkumar et al. describes an alternative approach to skeletal tissue repair using extracellular matrix (ECM) deposited by genetically modified mesenchymal stromal/stem cells. Here, they generate a loss of function mutations in VEGF or RUNX2 in a BMP2overexpressing MSC line and define the differences in the resulting tissue-engineered constructs following seeding onto a type I collagen matrix in vitro, and following lyophilization and subcutaneous and orthotopic implantation into mice and rats. Some strengths of this manuscript are the establishment of a platform by which modifications in cell-derived ECM can be evaluated both in vitro and in vivo, the demonstration that genetic modification of cells results in complexity of in vitro cell-derived ECM that elicits quantifiable results, and the admirable goal to improve endogenous cartilage repair. However, I recommend the authors clarify their conclusions and add more information regarding reproducibility, which was one limitation of primary-cell-derived ECMs. 

We thank the reviewer for the positive evaluation of our work.  

Overcoming the limitations of native/autologous/allogeneic ECMs such as complete decellularization and reduction of batch-to-batch variability was not specifically addressed in the data provided herein. For the maintenance of ECM organization and complexity following lyophilization, evidence of complete decellularization was not addressed, but could be easily evaluated using polarized light microscopy and quantification of human DNA for example in constructs pre and post-lyophilization. 

We appreciate the reviewer comments and acknowledge the lack of information in the first version of our manuscript. In line with our previous study (Pigeot et al., Advanced Materials 2021), the ectopic evaluation of our cartilage pellets was strictly done with lyophilized tissues using immunocompromised animals. Lyophilized tissues are thus considered devitalized, and not decellularized. Instead, the osteochondral defect experiment was performed with decellularized tissues in order to be able to implant the grafts in the rat immuno-competent model. This is now specified consistently throughout the manuscript. The decellularization process is also now incorporated accordingly in the method section (page 14, paragraph 2). We also provide quantifications of GAGs and DNAs from tissue pre- and post-decellularization (Supplementary figure 6A and 6B), described in the result section of the manuscript (page 9, paragraph 1). The decellularization step led to 97-98% of DNA removal.

Importantly, we do not claim full maintenance of ECM integrity following lyophilization nor decellularization.  This is now clarified in the discussion (page 12, paragraph 2). However, we report their capacity to instruct skeletal regeneration in multiple contexts despite extensive processing.

It would be ideal to see minimization of batch-to-batch variability using this approach, as mitigation of using a sole cell line is likely not sufficient (considering that the sole cell line-derived Matrigel does exhibit batch-to-batch and manufacturer-to-manufacturer variability). I recommend adding details regarding experimental design and outcomes not initially considered. Inter- and intraexperimental reproducibility was not adequately addressed. The size of in vitro-derived cartilage pellets was not quantified, and it is not clear that more than one independent 'differentiation' was performed from each gene-edited MSC line to generate in vitro replicates and constructs that were implanted in vivo. 

We thank the Reviewer for the comment on variability/reproducibility concern. Using a cell line does confer higher robustness but indeed does not grant unlimited consistency of batch production. We now temper our claims in the discussion and mention the need to regularly recharacterize cell lines properties upon passages (page 12, paragraph 2). Using our edited lines, we have generated multiple batches of cartilage grafts for their in vitro characterization or in vivo performance assessment. We have now compiled batch variations of GAG content and pellet volume, provided as Supplementary figure 5. This revealed that batches are indeed not identical (nor each pellets), but the production remains consistent.

The use of descriptive language in describing conclusions may mislead the reader and should be modified accordingly throughout the manuscript. For example, although this reviewer agrees with the comparative statements made by the authors regarding parental and gene-edited MSC lines, non-quantifiable terms such as 'frank' 'superior' (example, line 242) are inappropriate and should rather be discussed in terms of significance. Another example is 'rich-collagenous matrix,' which was not substantiated by uniform immunostaining for type II collagen (line 189). 

We thank the Reviewer for the constructive suggestions. We have revised the language accordingly throughout the manuscript. 

I have similar recommendations regarding conclusive statements from the rat implantation model, which was appropriately used for the purpose of evaluating the response of native skeletal cells to the different cell-derived ECMs. Interpretations of these results should be described with more accuracy. For example, increased TRAP staining does not indicate reduced active bone formation (line 237). Many would not conclude that GAGs were retained in the RUNX2-KO line graft subchondral region based on the histology. Quantification of % chondral regeneration using histology is not accurate as it is greatly influenced by the location in the defect from which the section was taken. Chondral regeneration is usually semi-quantified from gross observations of the cartilage surface immediately following excision. The statements regarding integration (example line 290) are not founded by histological evidence, which should show high magnification of the periphery of the graft adjacent to the native tissue. 

We have revised our language relative to the TRAP staining description (page 9, paragraph 2). We also agree with the reviewer on the semi-quantitative approach of our methodology,  which we transparently disclosed both in the main text (page 9, paragraph 3) and method section (page 18, paragraph 2). The sectioning location does influence the analysis, but to prevent this we performed an assessment at different depth (top, middle, bottom for each sample). This is now implemented in our method section (page 18, paragraph 3). On the tissue integration, we now provide higher magnification images of the implant/host tissue area (Figure 5F).

Reviewer #3 (Public Review): 

Summary: 

In this study, the authors have started off using an immortalized human cell line and then geneedited it to decrease the levels of VEGF1 (in order to influence vascularization), and the levels of Runx2 (to decrease chondro/osteogenesis). They first transplanted these cells with a collagen scaffold. The modified cells showed a decrease in vascularization when VEGF1 was decreased, and suggested an increase in cartilage formation. 

In another study, the matrix generated by these cells was subsequently remodeled into a bone marrow organ. When RUNX2 was decreased, the cells did not mineralize in vitro, and their matrices expressed types I and II collagen but not type X collagen in vitro, in comparison with unedited cells. In vivo, the author claims that remodeling of the matrices into bone was somewhat inhibited. Lastly, they utilized matrices generated by RUNX2 edited cells to regenerate chondro-osteal defects. They suggest that the edited cells regenerated cartilage in comparison with unedited cells. 

Strengths: 

- The notion that inducing changes in the ECM by genetically editing the cells is a novel one, as it has long been thought that ECM composition influences cell activity. 

- If successful, it may be possible to make off-the-shelf ECMS to carry out different types of tissue repair. 

We thank the Reviewer for the critical evaluation of our work and the highlighted novelty of it.  

Weaknesses: 

- The authors have not generated histologically identifiable cartilage or bone in their transplants of the cells with a type I scaffold. 

The chondrogenic differentiation of our MSOD-B line and their capacity of undergoing endochondral ossification has been robustly demonstrated in previous studies (Pigeot et al., Advanced Materials 2021 and Grigoryan et al., Science Translational Medicine 2022). In the present manuscript, we thus compare the chondrogenic capacity of newly established VEGF-KO and RUNX-KO lines to those of MSOD-B. We demonstrate by qualitative (Safranin-O staining, Collagen type 2 and Collagen type X immuno-stainings) and quantitative (glycosaminoglycans assay) assays that the generated tissues consist in cartilage tissue of similar quality than the MSOD-B. Of note, the safranin-O stainings were performed on lyophilized tissues, which can alter the staining quality/intensity. We now provide here additional stainings of generated tissues pre-lyophilization. This is implemented in Figure 1D and Figure 3D.

On the contested formation of bone in vivo by our ECMs grafts, we have provided compelling qualitative evidence via Masson´s Trichrome stainings and quantification of mineralized volume by µCT. Both cortical bone and trabecular structures were identified ectopically. Those are standard evaluation methods in the field, we would be happy to receive additional suggestions by the Reviewer. 

- In many cases, they did not generate histologically identifiable cartilage with their cell-free-edited scaffold. They did generate small amounts of bone but this is most likely due to BMPs that were synthesized by the cells and trapped in the matrix. 

We now appreciate that the Reviewer agrees on the successful formation of bone induced by our engineered grafts. We however still respectfully disagree with the “small amount of bone” statement since our MSOD-B and MSOD-B VEGF KO cartilage grafts led to the full generation of a mature ectopic bone organ (that is, also composed of extensive marrow). This has been assessed qualitatively and quantitatively. 

We agree with the Reviewer on the key role of BMP-2 in the remodeling process into bone and bone marrow, which we have extensively described in our previous publication (Pigeot et al., Advanced Materials 2021). However, the low amount of BMP-2 (in the dozens of nanogram/tissue range) embedded in the matrix is not sufficient per se to induce ectopic endochondral ossification. It is the combined presence of GAGs in the matrix -thus cartilage- that allows the success of bone formation.  

- There is a great deal of missing detail in the manuscript. 

We have incorporated additional methodological details describing the lyophilization/decellularization process of our tissues prior to evaluation (see Material and Methods section). We also have included a description of the MSOD-B line and implemented genetic elements (Supplementary Figure 1A).  

- The in vivo study is underpowered, the results are not well documented pictorially, and are not convincing. 

We believe our group size supports our conclusions confirmed by statistical assessment. We have provided additional stainings and images of higher magnifications (Figure 5) for both the ectopic and orthotopic in vivo evaluation.  

- Given the fact that they have genetically modified cells, they could have done analyses of ECM components to determine what was different between the lines, both at the transcriptome and the protein level. Consequently, the study is purely descriptive and does not provide any mechanistic understanding of what mixture of matrix components and growth factors works best for cartilage or bone. But this presupposes that they actually induced the formation of bona fide cartilage, at least. 

We thank the Reviewer for the suggestion. However, our study did not aim at understanding what ECM graft composition work best for cartilage nor bone regeneration respectively. Instead, we propose the exploitation of our cellular tools to interrogate the function of key ECM constituents and their impact in skeletal regeneration. We once more confirm that we generated cartilage grafts which is now better supported by additional histological assessment before lyophilization.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

In their previous publication (Dong et al. Cell Reports 2024), the authors showed that citalopram treatment resulted in reduced tumor size by binding to the E380 site of GLUT1 and inhibiting the glycolytic metabolism of HCC cells, instead of the classical citalopram receptor. Given that C5aR1 was also identified as the potential receptor of citalopram in the previous report, the authors focused on exploring the potential of the immune-dependent anti-tumor effect of citalopram via C5aR1. C5aR1 was found to be expressed on tumor-associated macrophages (TAMs) and citalopram administration showed potential to improve the stability of C5aR1 in vitro. Through macrophage depletion and adoptive transfer approaches in HCC mouse models, the data demonstrated the potential importance of C5aR1-expressing macrophage in the anti-tumor effect of citalopram in vivo. Mechanistically, their in vitro data suggested that citalopram may regulate the phagocytosis potential and polarization of macrophages through C5aR1. Next, they tried to investigate the direct link between citalopram and CD8+T cells by including an additional MASH-associated HCC mouse model. Their data suggest that citalopram may upregulate the glycolytic metabolism of CD8+T cells, probability via GLUT3 but not GLUT1-mediated glucose uptake. Lastly, as the systemic 5-HT level is down-regulated by citalopram, the authors analyzed the association between a low 5-HT and a superior CD8+T cell function against a tumor. Although the data is informative, the rationale for working on additional mechanisms and logical links among different parts is not clear. In addition, some of the conclusion is also not fully supported by the current data.

Thanks very much for your insightful evaluation and the constructive suggestions. We have thoroughly studied the comments and a provisional point-to-point response is shown as follows.

Strengths:

The idea of repurposing clinical-in-used drugs showed great potential for immediate clinical translation. The data here suggested that the anti-depression drug, citalopram displayed an immune regulatory role on TAM via a new target C5aR1 in HCC.

Thank you for your constructive comments. We believe that further investigation into the mechanisms by which citalopram modulates TAM function could provide valuable insights into its potential role in HCC therapy.

Weaknesses:

(1) The authors concluded that citalopram had a 'potential immune-dependent effect' based on the tumor weight difference between Rag-/- and C57 mice in Figure 1. However, tumor weight differences may also be attributed to a non-immune regulatory pathway. In addition, how do the authors calculate relative tumor weight? What is the rationale for using relative one but not absolute tumor weight to reflect the anti-tumor effect?

We appreciate your insights into the potential contributions of non-immune regulatory pathways to the observed tumor weight differences between Rag-/- and C57 mice, and we will further address this issue in our discussion. The relative tumor weight was calculated by assigning an arbitrary value of 1 to the Rag1^-/- mice in the DMSO treatment group, with all other tumor weights expressed relative to this baseline. As suggested, we will include absolute tumor weight data in our revised manuscript.

(2) The authors used shSlc6a4 tumor cell lines to demonstrate that citalopram's effects are independent of the conventional SERT receptor (Figure 1C-F). However, this does not entirely exclude the possibility that SERT may still play a role in this context, as it can be expressed in other cells within the tumor microenvironment. What is the expression profiling of Slc6a4 in the HCC tumor microenvironment? In addition, in Figure 1F, the tumor growth of shSlc6a4 in C57 mice displayed a decreased trend, suggesting a possible role of Slc6a4.

To identify the expression patterns of Slc6a4 in different cellular contexts within the HCC tumor microenvironment, we will conduct a thorough screening of HCC datasets that include single-cell sequencing analysis. The possible role of Slc6a4 on tumor growth will be verified with in vitro loss-of-function experiments.

(3) Why did the authors choose to study phagocytosis in Figures 3G-H? As an important player, TAM regulates tumor growth via various mechanisms.

Thank you for your question. We focused on this aspect because citalopram targets C5aR1-expressing TAM. C5aR1 is a receptor for complement component C5a, and complement components play a significant role in mediating the phagocytosis process in macrophages. In the revised manuscript, we will emphasize this rationale clearly.

(4) The information on unchanged deposition of C5a has been mentioned in this manuscript (Figures 3D and 3F), the authors should explain further in the manuscript, for example, C5a could bind to receptors other than C5aR1 and/or C5a bind to C5aR1 by different docking anchors compared with citalopram.

Thank you for your insightful comment. First, we will investigate the docking anchors involved in the binding of C5a to C5aR1 and compare these interactions with those of C5aR1 and citalopram. Additionally, we will discuss the potential binding of C5a to other receptors, providing a broader perspective on the signaling mechanisms.

(5) Figure 3I-M - the flow cytometry data suggested that citalopram treatment altered the proportions of total TAM, M1 and M2 subsets, CD4+ and CD8+T cells, DCs, and B cells. Why does the author conclude that the enhanced phagocytosis of TAM was one of the major mechanisms of citalopram? As the overall TAM number was regulated, the contribution of phagocytosis to tumor growth may be limited.

As suggested, we will restate the conclusion to enhance clarity and better articulate the relationship between citalopram treatment, TAM populations, and their phagocytic activity. Thank you for your valuable input.

(6) Figure 4 - what is the rationale for using the MASH-associated HCC mouse model to study metabolic regulation in CD8+T cells? The tumor microenvironment and tumor growth would be quite different. In addition, how does this part link up with the mechanisms related to C5aR1 and TAM? The authors also brought GLUT1 back in the last part and focused on CD8+T cell metabolism, which was totally separated from previous data.

We chose the MASH-associated HCC mouse model because it closely mimics the etiology of metabolic-associated fatty liver disease (MAFLD), which is a significant contributor to the development of cirrhosis and HCC. The inclusion of CD8⁺ T cells in our study is based on the understanding that citalopram targets GLUT1, which plays a crucial role in glucose uptake. CD8⁺ T cell function is heavily reliant on glycolytic metabolism, making it essential to investigate how citalopram’s effects on GLUT1 influence the metabolic pathways and functionality of these immune cells. The data presented in this section primarily aim to demonstrate how citalopram influences peripheral 5-HT levels, which subsequently affects CD8⁺ T cell functionality. By linking these findings, we will clarify how citalopram impacts both TAM and CD8⁺ T cells. In the revised manuscript, we will enhance the background information and provide relevant data support to avoid any gaps.

(7) Figure 5, the authors illustrated their mechanism that citalopram regulates CD8+T cell anti-tumor immunity through proinflammatory TAM with no experimental evidence. Using only CD206 and MHCII to represent TAM subsets obviously is not sufficient.

As suggested, more relevant experimental data will be included in the revised manuscript to better characterize the TAM populations and their roles in mediating the effects of citalopram on CD8⁺ T cells.

Reviewer #2 (Public review):

Summary:

Dong et al. present a thorough investigation into the potential of repurposing citalopram, an SSRI, for hepatocellular carcinoma (HCC) therapy. The study highlights the dual mechanisms by which citalopram exerts anti-tumor effects: reprogramming tumor-associated macrophages (TAMs) toward an anti-tumor phenotype via C5aR1 modulation and suppressing cancer cell metabolism through GLUT1 inhibition while enhancing CD8+ T cell activation. The findings emphasize the potential of drug repurposing strategies and position C5aR1 as a promising immunotherapeutic target. However, certain aspects of experimental design and clinical relevance could be further developed to strengthen the study's impact.

Thank you for your thoughtful review and constructive feedback, and we look forward to improving our manuscript accordingly.

Strength:

It provides detailed evidence of citalopram's non-canonical action on C5aR1, demonstrating its ability to modulate macrophage behavior and enhance CD8+ T cell cytotoxicity. The use of DARTS assays, in silico docking, and gene signature network analyses offers robust validation of drug-target interactions. Additionally, the dual focus on immune cell reprogramming and metabolic suppression presents a thorough strategy for HCC therapy. By emphasizing the potential for existing drugs like citalopram to be repurposed, the study also underscores the feasibility of translational applications.

Your insights reinforce the significance of our findings, and we will ensure that these points are clearly articulated in the revised manuscript to enhance its impact.

Major weaknesses/suggestions:

The dataset and signature database used for GSEA analyses are not clearly specified, limiting reproducibility. The manuscript does not fully explore the potential promiscuity of citalopram's interactions across GLUT1, C5aR1, and SERT1, which could provide a deeper understanding of binding selectivity. The absence of GLUT1 knockdown or knockout experiments in macrophages prevents a complete assessment of GLUT1's role in macrophage versus tumor cell metabolism. Furthermore, there is minimal discussion of clinical data on SSRI use in HCC patients. Incorporating survival outcomes based on SSRI treatment could strengthen the study's translational relevance.

By addressing these limitations, the manuscript could make an even stronger contribution to the fields of cancer immunotherapy and drug repurposing.

We appreciate your valuable suggestions. As suggested, we will take the following actions:

(1) GSEA analysis: we will clearly specify the datasets and signature databases used for the GSEA in the revised manuscript.

(2) Exploration of binding selectivity: we recognize the importance of exploring the potential promiscuity of citalopram’s interactions across GLUT1, C5aR1, and SERT1. As suggested, we will include a more detailed analysis of these interactions, which will help elucidate binding selectivity and its implications for therapeutic outcomes.

(3) GLUT1 knockdown in macrophages: to address the gap in our assessment of GLUT1’s role in macrophages, we will incorporate GLUT1 knockdown or knockout experiments in macrophages upon citalopram treatment. Moreover, a DARTS assay for GLUT1 in THP-1 cells will be conducted.

(4) Clinical data on SSRI use in HCC patients: Related data have been reported previously in PMID: 39388353 (Cell Rep. 2024 Oct 22;43(10):114818.). As detailed below:

“SSRIs use is associated with reduced disease progression in HCC patients

We determined whether SSRIs for alleviating HCC are supported by real-world data. A total of 3061 patients with liver cancer were extracted from the Swedish Cancer Register. Among them, 695 patients had been administrated with post-diagnostic SSRIs. The Kaplan-Meier survival analysis suggested that patients who utilized SSRIs exhibited a significantly improved metastasis-free survival compared to those who did not use SSRIs, with a P value of log-rank test at 0.0002. Cox regression analysis showed that SSRI use was associated with a lower risk of metastasis (HR = 0.78; 95% CI, 0.62-0.99).”

Author response image 1.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

In a previous work, Prut and colleagues had shown that during reaching, high-frequency stimulation of the cerebellar outputs resulted in reduced reach velocity. Moreover, they showed that the stimulation produced reaches that deviated from a straight line, with the shoulder and elbow movements becoming less coordinated. In this report, they extend their previous work by the addition of modeling results that investigate the relationship between the kinematic changes and torques produced at the joints. The results show that the slowing is not due to reductions in interaction torques alone, as the reductions in velocity occur even for movements that are single joints. More interestingly, the experiment revealed evidence for the decomposition of the reaching movement, as well as an increase in the variance of the trajectory.

Strengths:

This is a rare experiment in a non-human primate that assessed the importance of cerebellar input to the motor cortex during reaching.

Weaknesses:

My major concerns are described below.

If I understand the task design correctly, the monkeys did not need to stop their hand at the target. I think this design may be suboptimal for investigating the role of the cerebellum in control of reaching because a number of earlier works have found that the cerebellum's contributions are particularly significant as the movement ends, i.e., stopping at the target. For example, in mice, interposed nucleus neurons tend to be most active near the end of the reach that requires extension, and their activation produces flexion forces during the reach (Becker and Person 2019). Indeed, the inactivation of interposed neurons that project to the thalamus results in overshooting of reaching movements (Low et al. 2018). Recent work has also found that many Purkinje cells show a burst-pause pattern as the reach nears its endpoint, and stimulation of the mossy fibers tends to disrupt endpoint control (Calame et al. 2023). Thus, the fact that the current paper has no data regarding endpoint control of the reach is puzzling to me.

We appreciate the reviewer’s point that cerebellar contributions can be particularly critical near the endpoint of a reach. In our current task design, monkeys were indeed required to hold at the target briefly—100 ms for Monkeys S and P, and 150 ms for Monkeys C and M—before receiving a reward. However, given the size of the targets and the velocity of movements, it often happened that the monkey didn’t have to stop its movement to obtain a reward. Importantly, we relaxed the task’s requirements (by increasing target size and reducing temporal constraints) to allow monkeys to perform the task under cerebellar block conditions as we found that the strict criteria in these conditions yield a low success rate. This design is suboptimal for studying endpoint accuracy which, as we now appreciate, is an important aspect of cerebellar control. In our revision, we will clarify these aspects of the task design and acknowledge that it is sub-optimal for examining the role of cerebellum in end-point control. Future studies will explicitly address this point more carefully.

Because stimulation continued after the cursor had crossed the target, it is interesting to ask whether this disruption had any effects on the movements that were task-irrelevant. The reason for asking this is because we have found that whereas during task-relevant eye or tongue movements the Purkinje cells are strongly modulated, the modulations are much more muted when similar movements are performed but are task-irrelevant (Pi et al., PNAS 2024; Hage et al. Biorxiv 2024). Thus, it is interesting to ask whether the effects of stimulation were global and affected all movements, or were the effects primarily concerned with the task-relevant movements.

This is a very interesting suggestion. Although our main analysis focused on target-directed reaching movements, we have the data for the between-trial movements under continuous stimulation (e.g., return to center movements). In our revised supplementary material, we will examine the effect of cerebellar block on endpoint velocities in inter-trial movements versus task-related movements.

If the schematic in Figure 1 is accurate, it is difficult for me to see how any of the reaching movements can be termed single joint. In the paper, T1 is labeled as a single joint, and T2-T4 are labeled as dual-joint. The authors should provide data to justify this.

The is reviewer right and movements to all targets engages shoulder and elbow but the single joint participation varied in a target-specific manner. In the manuscript, we used the term “single-joint” to indicate a target direction in which one joint remains stationary, resulting in minimal coupling torque at the adjacent joint. Specifically, for Targets 1 and 5 in our experiments, the net torque (and thus acceleration) at the elbow was negligible, and hence the shoulder experienced correspondingly low coupling torque (as illustrated in Figure 3c of our manuscript). To avoid confusion, we will use the term ‘predominantly single-joint’ movements in our revised manuscript to indicate targets with low coupling torques. We will also include an additional figure in the revised supplementary material displaying the net torques at the shoulder and elbow, similar to Figures 2c and 3c. Our goal is to demonstrate that movements to targets 1 and 5 are characterized by predominantly one-joint engagement (i.e., the elbow is stationary with low net torque) and low coupling torques, rather than implying a purely isolated, single-joint motion.

Because at least part of this work was previously analyzed and published, information should be provided regarding which data are new.

We will include a clear statement in the Methods section specifying which components of the dataset and analyses are entirely new. While some of the same animals and stimulation protocol were presented in prior work, the inverse-dynamics modeling, analyses of progressive movement changes across trials under stimulation and invariance of motor noise to movement velocity are newly reported in this manuscript.

Reviewer #2 (Public review):

This manuscript asks an interesting and important question: what part of 'cerebellar' motor dysfunction is an acute control problem vs a compensatory strategy to the acute control issue? The authors use a cerebellar 'blockade' protocol, consisting of high-frequency stimuli applied to the cerebellar peduncle which is thought to interfere with outflow signals. This protocol was applied in monkeys performing center outreaching movements and has been published from this laboratory in several preceding studies. I found the take-home-message broadly convincing and clarifying - that cerebellar block reduces muscle activation acutely particularly in movements that involve multiple joints and therefore invoke interaction torques, and that movements progressively slow down to in effect 'compensate' for these acute tone deficits. The manuscript was generally well written, and the data was clear, convincing, and novel. My comments below highlight suggestions to improve clarity and sharpen some arguments.

Primary comments:

(1) Torque vs. tone: Is it known whether this type of cerebellar blockade is reducing muscle tone or inducing any type of acute co-contraction that could influence limb velocity through mechanisms different than 'atonia'? If so, the authors should discuss this information in the discussion section starting around line 336, and clarify that this motivates (if it does) the focus on 'torques' rather than muscle activation. Relatedly, besides the fact that there are joints involved, is there a reason there is so much emphasis on torque per se? If the muscle is deprived of sufficient drive, it would seem that it would be more straightforward to conceptualize the deficit as one of insufficient timed drive to a set of muscles than joint force. Some text better contextualizing the choices made here would be sufficient to address this concern. I found statements like those in the introduction "hand velocity was low initially, reflecting a primary muscle torque deficit" to be lacking in substance. Either that statement is self-evident or the alternative was not made clear. Finally, emphasize that it is a loss of self-generated torque at the shoulder that accounts for the velocity deficits. At times the phrasing makes it seem that there is a loss of some kind of passive torque.

We appreciate the reviewer’s emphasis on distinguishing reduced muscle tone and altered co-contraction patterns as possible explanations for decreased limb velocity. Our focus on torques arises from previous studies suggesting that the core deficit in cerebellar ataxia is impaired prediction of coupling torques. This point will be added in the discussion section of our revised manuscript where we will explain why we prioritize muscle torques and how muscle-level activation collectively contributes to net joint torques. Also, we will underscore that the observed velocity deficits primarily reflect a reduction of self-generated torque at the shoulder (whether acute or adaptive), rather than any reduction in passive torques.

(2) Please clarify some of the experimental metrics: Ln 94 RESULTS. The success rate is used as a primary behavioral readout, but what constitutes success is not clearly defined in the methods. In addition to providing a clear definition in the methods section, it would also be helpful for the authors to provide a brief list of criteria used to determine a 'successful' movement in the results section before the behavioral consequences of stimulation are described. In particular, the time and positional error requirements should be clear.

Successful trials were trials in which monkeys didn’t leave the center position before the go signal and reached the peripheral target within a specific time criteria. These values varied in different monkeys. We will include detailed definitions of our success criteria in the revised methods section of our manuscript. Specifically, we will update our methods section to include (i) the timing criteria of each phase of the trials and (ii) the size of the peripheral targets indicating the tolerance for endpoint accuracy.

(3) Based on the polar plot in Figure 1c, it seemed odd to consider Targets 1-4 outward and 5-8 inward movements, when 1 and 5 are side-to-side. Is there a rationale for this grouping or might results be cleaner by cleanly segregating outward (targets 2-4) and inward (targets 6-8) movements? Indeed, by Figure 3 where interaction torques are measured, this grouping would seem to align with the hypothesis much more cleanly since it is with T2,T3,and T4 where clear coupling torques deficits are seen with cerebellar block.

We acknowledge the reviewer’s observation regarding Targets 1 and 5 being side-to-side rather than strictly “outward” or “inward.” In the first section of our results, we grouped the targets in this way to emphasize the notably stronger effect of the cerebellar block on targets involving shoulder flexion (‘outward’) as compared to those involving shoulder extension (‘inwards’). For subsequent analyses we focused on the effects of cerebellar block on outward targets where movements were single-joint (Target 1) vs. multi-joint (Targets 2-4). To clarify this aspect, in our revised manuscript we will explain the rationale for grouping T1–T4 as “outward” and T5–T8 as “inward,” including how we defined them.

(4) I did not follow Figure 3d. Both the figure axis labels and the description in the main text were difficult to follow. Furthermore, the color code per animal made me question whether the linear regression across the entire dataset was valid, or would be better performed within animal, and the regressions summarized across animals. The authors should look again at this section and figure.

We will revise the figure labels and legend to clarify how each axis is defined. Please note that pooling the data was done after confirming that data from each animal expressed a similar trend. Specifically, the correlation coefficients were all positive but statistically significant in 3 out of the 4 monkeys. Moreover, following the reviewers’ feedback, we also did a partial correlation analysis (which controls for the variability across monkeys) and found a significant correlation (r = 0.33, p < 0.001). These points will be described in the revised manuscript.

(5) Line 206+ The rationale for examining movement decomposition with a cerebellar block is presented as testing the role of the cerebellum in timing. Yet it is not spelled out what movement decomposition and trajectory variability have to do with motor timing per se.

The reviewer is right and the relations between timing, decomposition and variability need to be explicitly presented. In our revision, we will explain how decomposed movements may reflect impaired temporal coordination across multiple joints—a critical cerebellar function. We will also clarify how increased variability in joint coordination can result in increased trial-to-trial variability of trajectories.

Reviewer #3 (Public review):

Summary:

In their manuscript, "Disentangling acute motor deficits and adaptive responses evoked by the loss of cerebellar output," Sinha and colleagues aim to identify distinct causes of motor impairments seen when perturbing cerebellar circuits. This goal is an important one, given the diversity of movement-related phenotypes in patients with cerebellar lesions or injuries, which are especially difficult to dissect given the chronic nature of the circuit damage. To address this goal, the authors use high-frequency stimulation (HFS) of the superior cerebellar peduncle in monkeys performing reaching movements. HFS provides an attractive approach for transiently disrupting cerebellar function previously published by this group. First, they found a reduction in hand velocities during reaching, which was more pronounced for outward versus inward movements. By modeling inverse dynamics, they find evidence that shoulder muscle torques are especially affected. Next, the authors examine the temporal evolution of movement phenotypes over successive blocks of HFS trials. Using this analysis, they find that in addition to the acute, specific effects on muscle torques in early HFS trials, there was an additional progressive reduction in velocity during later trials, which they interpret as an adaptive response to the inability to effectively compensate for interaction torques during cerebellar block. Finally, the authors examine movement decomposition and trajectory, finding that even when low-velocity reaches are matched to controls, HFS produces abnormally decomposed movements and higher than expected variability in trajectory.

Strengths:

Overall, this work provides important insight into how perturbation of cerebellar circuits can elicit diverse effects on movement across multiple timescales.

The HFS approach provides temporal resolution and enables analysis that would be hard to perform in the context of chronic lesions or slow pharmacological interventions. Thus, this study describes an important advance over prior methods of circuit disruption, and their approach can be used as a framework for future studies that delve deeper into how additional aspects of sensorimotor control are disrupted (e.g., response to limb perturbations).

In addition, the authors use well-designed behavioral approaches and analysis methods to distinguish immediate from longer-term adaptive effects of HFS on behavior. Moreover, inverse dynamics modeling provides important insight into how movements with different kinematics and muscle dynamics might be differentially disrupted by cerebellar perturbation.

Weaknesses:

The argument that there are acute and adaptive effects to perturbing cerebellar circuits is compelling, but there seems to be a lost opportunity to leverage the fast and reversible nature of the perturbations to further test this idea and strengthen the interpretation. Specifically, the authors could have bolstered this argument by looking at the effects of terminating HFS - one might hypothesize that the acute impacts on muscle torques would quickly return to baseline in the absence of HFS, whereas the longer-term adaptive component would persist in the form of aftereffects during the 'washout' period. As is, the reversible nature of the perturbation seems underutilized in testing the authors' ideas.

We agree that our approach could more explicitly exploit the rapid reversibility of high-frequency stimulation (HFS) by examining post-stimulation ‘washout’ periods. However, for the present dataset, we ended the session after the set of cerebellar block trials. We plan to study the effect of cerebellar block on immediate post-block washout trials in the future.  

The analysis showing that there is a gradual reduction in velocity during what the authors call an adaptive phase is convincing. That said, the argument is made that this is due to difficulty in compensating for interaction torques. Even if the inward targets (i.e., targets 6-8) do not show a deficit during the acute phase, these targets still have significant interaction torques (Figure 3c). Given the interpretation of the data as presented, it is not clear why disruption of movement during the adaptive phase would not be seen for these targets as well since they also have large interaction torques. Moreover, it is difficult to delve into this issue in more detail, as the analyses in Figures 4 and 5 omit the inward targets.

The reviewer is right and movements to Targets 6–8 (inward) were seemingly unaffected despite also involving significant interaction torques. In fact, we have already attempted to address this issue in the discussion section of the version 1 of our manuscript. Specifically, we note that while outward targets (2–4) tend to involve higher coupling torque impulses on average, this alone does not fully explain the differential impact of cerebellar block, as illustrated by discrepancies at the individual target level (e.g., target 7 vs. target 1). We proposed two possible explanations: (1) a bias toward shoulder flexion in the effect of cerebellar block—consistent with earlier studies showing ipsilateral flexor activation or tone changes following stimulation or lesioning of the deep cerebellar nuclei; and (2) a posture-related facilitation of inward (shoulder extension) movements from the central starting position.

The text in the Introduction and in the prior work developing the HFS approach overstates the selectivity of the perturbations. First, there is an emphasis on signals transmitted to the neocortex. As the authors state several times in the Discussion, there are many subcortical targets of the cerebellar nuclei as well, and thus it is difficult to disentangle target-specific behavioral effects using this approach. Second, the superior cerebellar peduncle contains both cerebellar outputs and inputs (e.g., spinocerebellar). Therefore, the selectivity in perturbing cerebellar output feels overstated. Readers would benefit from a more agnostic claim that HFS affects cerebellar communication with the rest of the nervous system, which would not affect the major findings of the study.

The reviewer is right that the superior cerebellar peduncle carries both descending and ascending fibers, and that cerebellar nuclei project to subcortical as well as cortical targets. However, it is also important to note that in primates the cerebellar-thalamo-cortical (CTC) pathway greatly expanded (on the expanse of the cerbello-rubro-spinal tract) in mediating cerebellar control of voluntary movements (Horne and Butler, 1995). The cerebello-subcortical pathways lost its importance over the course of evolution (Nathan and Smith, 1982, Padel et al., 1981, ten Donkelaar, 1988). In our previous study we found that the ascending spinocerebellar axons which enter the cerebellum through the SCP are weakly task-related and the descending system is quite small (Cohen et al, 2017). However, we cannot rule out an effect of HFS mediated in part through other systems. In the revised introduction section, we will clarify this point and use more careful language about the scope of our stimulation, emphasizing that HFS disrupts cerebellar communication broadly, rather than solely the cerebello-thalamo-cortical pathway.

The text implies that increased movement decomposition and variability must be due to noise. However, this assumption is not tested. It is possible that the impairments observed are caused by disrupted commands, independent of whether these command signals are noisy. In other words, commands could be low noise but still faulty.

We recognize the reviewer’s concern about linking movement decomposition and trial-to-trial trajectory variability with motor noise. As presented in our discussion section, we interpret these motor abnormalities as a form of motor noise in the sense that they are generated by faulty motor commands. We draw our interpretation from the findings of previous research work which show that the cerebellum aids in the state estimation of the limb and subsequent generation of accurate feedforward commands. Therefore, disruption of the cerebellar output may lead to faulty motor commands resulting in the observed asynchronous joint activations (i.e., movement decomposition) and unpredictable trajectories (i.e., increased trial-to-trial variability). Both observed deficits resemble increased motor noise.

Throughout the text, the use of the term 'feedforward control' seems unnecessary. To dig into the feedforward component of the deficit, the authors could quantify the trajectory errors only at the earliest time points (e.g., in Figure 5d), but even with this analysis, it is difficult to disentangle feedforward- and feedback-mediated effects when deficits are seen throughout the reach. While outside the scope of this study, it would be interesting to explore how feedback responses to limb perturbation are affected in control versus HFS conditions. However, as is, these questions are not explored, and the claim of impaired feedforward control feels overstated.

We agree that to strictly focus on feedforward control, we could have examined the measured variables in the first 50-100 ms of the movement which has been shown to be unaffected by feedback responses (Pruszynski et al. 2008, Todorov and Jordan 2002, Pruszynski and Scott 2012, Crevecoeur et al. 2013). However, in our task the amplitude of movements made by our monkeys was small and therefore the response measures we used were too small in the first 50-100 ms for a robust estimation. Also, fixing a time window led to an unfair comparison between control and cerebellar block trials, in which velocity was significantly reduced and therefore movement time was longer. Therefore, we used the peak velocity, torque-impulse at the peak velocity and maximum deviation of the hand trajectory as response measures. We will acknowledge this point in the discussion section of our revised manuscript. We will also tone down references to feedforward control throughout the text of our revised manuscript as suggested by the reviewer.

The terminology 'single-joint' movement is a bit confusing. At a minimum, it would be nice to show kinematics during different target reaches to demonstrate that certain targets are indeed single joint movements. More of an issue, however, is that it seems like these are not actually 'single-joint' movements. For example, Figure 2c shows that target 1 exhibits high elbow and shoulder torques, but in the text, T1 is described as a 'single-joint' reach (e.g. lines 155-156). The point that I think the authors are making is that these targets have low interaction torques. If that is the case, the terminology should be changed or clarified to avoid confusion.

Indeed, as reviewer #1 also noted, movements to target 1 and 5 are not purely single-joint but rather have relatively low coupling torques. Our intention while using the term “single-joint” was to indicate a target direction in which one joint remains stationary, resulting in minimal coupling torque at the adjacent joint. Specifically, for Targets 1 and 5 in our experiments, the net torque (and thus acceleration) at the elbow was negligible, and hence the shoulder experienced correspondingly low coupling torque (as illustrated in Figure 3c of our manuscript). ). To avoid confusion, we will use the term ‘predominantly single-joint’ movements in our revised manuscript to indicate targets with low coupling torques. We will also include an additional figure in the revised supplementary material displaying the net torques at the shoulder and elbow, similar to Figures 2c and 3c. Our goal is to demonstrate that movements to targets 1 and 5 are characterized by predominantly one-joint engagement (i.e., the elbow is stationary with low net torque) and low coupling torques, rather than implying a purely isolated, single-joint motion.

The labels in Figure 3d are confusing and could use more explanation in the figure legend.

In Figure 3d, it is stated that data from all monkeys is pooled. However, if there is a systematic bias between animals, this could generate spurious correlations. Were correlations also calculated for each animal separately to confirm the same trend between velocity and coupling torques holds for each animal?

We will revise the figure legend and main-text explanation for Figure 3d. Please note that pooling the data was done after confirming that data from each animal expressed a similar trend. Specifically, the correlation coefficients were positive but significant for 3 out of the 4 monkeys. Moreover, following the reviewers’ feedback, we also did a partial correlation analysis (which controls for the variability across monkeys) and found a significant correlation (r = 0.33, p < 0.001). These points will be described in the revised manuscript.

In Table S1, it would be nice to see target-specific success rates. The data would suggest that targets with the highest interaction torques will have the largest reduction in success rates, especially during later HFS trials. Is this the case?

We will provide a breakdown of the success rates as a function of targets. However, one should note that success/failure may depend on several factors beyond impaired limb dynamics. In a previous study (Nashef et al. 2019) we identified several causes of failure such as (i) not entering the central target in time, (ii) moving out too early from the peripheral target, (iii) Reaction time longer than permitted, or (iv) premature exit from the central target before permitted.

Author response:

eLife Assessment

This valuable short paper is an ingenious use of clinical patient data to address an issue in imaging neuroscience. The authors clarify the role of face-selectivity in human fusiform gyrus by measuring both BOLD fMRI and depth electrode recordings in the same individuals; furthermore, by comparing responses in different brain regions in the two patients, they suggested that the suppression of blood oxygenation is associated with a decrease in local neural activity. While the methods are compelling and provide a rare dataset of potentially general importance, the presentation of the data in its current form is incomplete.

We thank the Reviewing editor and Senior editor at eLife for their positive assessment of our paper. After reading the reviewers’ comments – to which we reply below - we agree that the presentation of the data could be completed. We provide additional presentation of data in the responses below and we will slightly modify Figure 2 of the paper. However, in keeping the short format of the paper, the revised version will have the same number of figures, which support the claims made in the paper.

Reviewer #1 (Public review):

Summary:

Measurement of BOLD MR imaging has regularly found regions of the brain that show reliable suppression of BOLD responses during specific experimental testing conditions. These observations are to some degree unexplained, in comparison with more usual association between activation of the BOLD response and excitatory activation of the neurons (most tightly linked to synaptic activity) in the same brain location. This paper finds two patients whose brains were tested with both non-invasive functional MRI and with invasive insertion of electrodes, which allowed the direct recording of neuronal activity. The electrode insertions were made within the fusiform gyrus, which is known to process information about faces, in a clinical search for the sites of intractable epilepsy in each patient. The simple observation is that the electrode location in one patient showed activation of the BOLD response and activation of neuronal firing in response to face stimuli. This is the classical association. The other patient showed an informative and different pattern of responses. In this person, the electrode location showed a suppression of the BOLD response to face stimuli and, most interestingly, an associated suppression of neuronal activity at the electrode site.

Strengths:

Whilst these results are not by themselves definitive, they add an important piece of evidence to a long-standing discussion about the origins of the BOLD response. The observation of decreased neuronal activation associated with negative BOLD is interesting because, at various times, exactly the opposite association has been predicted. It has been previously argued that if synaptic mechanisms of neuronal inhibition are responsible for the suppression of neuronal firing, then it would be reasonable

Weaknesses:

The chief weakness of the paper is that the results may be unique in a slightly awkward way. The observation of positive BOLD and neuronal activation is made at one brain site in one patient, while the complementary observation of negative BOLD and neuronal suppression actually derives from the other patient. Showing both effects in both patients would make a much stronger paper.

We thank reviewer #1 for their positive evaluation of our paper. Obviously, we agree with the reviewer that the paper would be much stronger if BOTH effects – spike increase and decrease – would be found in BOTH patients in their corresponding fMRI regions (lateral and medial fusiform gyrus) (also in the same hemisphere). Nevertheless, we clearly acknowledge this limitation in the (revised) version of the manuscript (p.8: Material and Methods section).

In the current paper, one could think that P1 shows only increases to faces, and P2 would show only decreases (irrespective of the region). However, that is not the case since 11% of P1’s face-selective units are decreases (89% are increases) and 4% of P2’s face-selective units are increases. This has now been made clearer in the manuscript (p.5).

As the reviewer is certainly aware, the number and position of the electrodes are based on strict clinical criteria, and we will probably never encounter a situation with two neighboring (macro-micro hybrid electrodes), one with microelectrodes ending up in the lateral MidFG, the other in the medial MidFG, in the same patient. If there is no clinical value for the patient, this cannot be done.

The only thing we can do is to strengthen these results in the future by collecting data on additional patients with an electrode either in the lateral or the medial FG, together with fMRI. But these are the only two patients we have been able to record so far with electrodes falling unambiguously in such contrasted regions and with large (and comparable) measures.

While we acknowledge that the results may be unique because of the use of 2 contrasted patients only (and this is why the paper is a short report), the data is compelling in these 2 cases, and we are confident that it will be replicated in larger cohorts in the future.

Reviewer #2 (Public review):

Summary:

This is a short and straightforward paper describing BOLD fMRI and depth electrode measurements from two regions of the fusiform gyrus that show either higher or lower BOLD responses to faces vs. objects (which I will call face-positive and facenegative regions). In these regions, which were studied separately in two patients undergoing epilepsy surgery, spiking activity increased for faces relative to objects in the face-positive region and decreased for faces relative to objects in the face-negative region. Interestingly, about 30% of neurons in the face-negative region did not respond to objects and decreased their responses below baseline in response to faces (absolute suppression).

Strengths:

These patient data are valuable, with many recording sessions and neurons from human face-selective regions, and the methods used for comparing face and object responses in both fMRI and electrode recordings were robust and well-established. The finding of absolute suppression could clarify the nature of face selectivity in human fusiform gyrus since previous fMRI studies of the face-negative region could not distinguish whether face < object responses came from absolute suppression, or just relatively lower but still positive responses to faces vs. objects.

Weaknesses:

The authors claim that the results tell us about both 1) face-selectivity in the fusiform gyrus, and 2) the physiological basis of the BOLD signal. However, I would like to see more of the data that supports the first claim, and I am not sure the second claim is supported.

(1) The authors report that ~30% of neurons showed absolute suppression, but those data are not shown separately from the neurons that only show relative reductions. It is difficult to evaluate the absolute suppression claim from the short assertion in the text alone (lines 105-106), although this is a critical claim in the paper.

We thank reviewer #2 for their positive evaluation of our paper. We understand the reviewer’s point, and we partly agree. Where we respectfully disagree is that the finding of absolute suppression is critical for the claim of the paper: finding an identical contrast between the two regions in terms of RELATIVE increase/decrease of face-selective activity in fMRI and spiking activity is already novel and informative. Where we agree with the reviewer is that the absolute suppression could be more documented: it wasn’t, due to space constraints (brief report). We provide below an example of a neuron showing absolute suppression to faces. In the frequency domain, there is only a face-selective response (1.2 Hz and harmonics) but no significant response at 6 Hz (common general visual response). In the time-domain, relative to face onset, the response drops below baseline level. It means that this neuron has baseline (non-periodic) spontaneous spiking activity that is actively suppressed when a face appears.

Author response image 1.

(2) I am not sure how much light the results shed on the physiological basis of the BOLD signal. The authors write that the results reveal "that BOLD decreases can be due to relative, but also absolute, spike suppression in the human brain" (line 120). But I think to make this claim, you would need a region that exclusively had neurons showing absolute suppression, not a region with a mix of neurons, some showing absolute suppression and some showing relative suppression, as here. The responses of both groups of neurons contribute to the measured BOLD signal, so it seems impossible to tell from these data how absolute suppression per se drives the BOLD response.

It is a fact that we find both kinds of responses in the same region.  We cannot tell with this technique if neurons showing relative vs. absolute suppression of responses are spatially segregated for instance (e.g., forming two separate sub-regions) or are intermingled. And we cannot tell from our data how absolute suppression per se drives the BOLD response. In our view, this does not diminish the interest and originality of the study, but the statement "that BOLD decreases can be due to relative, but also absolute, spike suppression in the human brain” will be rephrased in the revised manuscript, in the following way: "that BOLD decreases can be due to relative, or absolute (or a combination of both), spike suppression in the human brain”.

Reviewer #3 (Public review):

In this paper the authors conduct two experiments an fMRI experiment and intracranial recordings of neurons in two patients P1 and P2. In both experiments, they employ a SSVEP paradigm in which they show images at a fast rate (e.g. 6Hz) and then they show face images at a slower rate (e.g. 1.2Hz), where the rest of the images are a variety of object images. In the first patient, they record from neurons over a region in the mid fusiform gyrus that is face-selective and in the second patient, they record neurons from a region more medially that is not face selective (it responds more strongly to objects than faces). Results find similar selectivity between the electrophysiology data and the fMRI data in that the location which shows higher fMRI to faces also finds face-selective neurons and the location which finds preference to non faces also shows non face preferring neurons.

Strengths:

The data is important in that it shows that there is a relationship between category selectivity measured from electrophysiology data and category-selective from fMRI. The data is unique as it contains a lot of single and multiunit recordings (245 units) from the human fusiform gyrus - which the authors point out - is a humanoid specific gyrus.

Weaknesses:

My major concerns are two-fold:

(i) There is a paucity of data; Thus, more information (results and methods) is warranted; and in particular there is no comparison between the fMRI data and the SEEG data.

We thank reviewer #3 for their positive evaluation of our paper. If the reviewer means paucity of data presentation, we agree and we provide more presentation below, although the methods and results information appear as complete to us. The comparison between fMRI and SEEG is there, but can only be indirect (i.e., collected at different times and not related on a trial-by-trial basis for instance). In addition, our manuscript aims at providing a short empirical contribution to further our understanding of the relationship between neural responses and BOLD signal, not to provide a model of neurovascular coupling.

(ii) One main claim of the paper is that there is evidence for suppressed responses to faces in the non-face selective region. That is, the reduction in activation to faces in the non-face selective region is interpreted as a suppression in the neural response and consequently the reduction in fMRI signal is interpreted as suppression. However, the SSVEP paradigm has no baseline (it alternates between faces and objects) and therefore it cannot distinguish between lower firing rate to faces vs suppression of response to faces.

We understand the concern of the reviewer, but we respectfully disagree that our paradigm cannot distinguish between lower firing rate to faces vs. suppression of response to faces. Indeed, since the stimuli are presented periodically (6 Hz), we can objectively distinguish stimulus-related activity from spontaneous neuronal firing. The baseline corresponds to spikes that are non-periodic, i.e., unrelated to the (common face and object) stimulation. For a subset of neurons, even this non-periodic baseline activity is suppressed, above and beyond the suppression of the 6 Hz response illustrated on Figure 2. We mention it in the manuscript, but we agree that we do not present illustrations of such decrease in the time-domain for SU, which we did not consider as being necessary initially (please see below for such presentation).

(1) Additional data: the paper has 2 figures: figure 1 which shows the experimental design and figure 2 which presents data, the latter shows one example neuron raster plot from each patient and group average neural data from each patient. In this reader's opinion this is insufficient data to support the conclusions of the paper. The paper will be more impactful if the researchers would report the data more comprehensively.

We answer to more specific requests for additional evidence below, but the reviewer should be aware that this is a short report, which reaches the word limit. In our view, the group average neural data should be sufficient to support the conclusions, and the example neurons are there for illustration. And while we cannot provide the raster plots for a large number of neurons, the anonymized data will be made available upon publication of the final version of the paper.

(a) There is no direct comparison between the fMRI data and the SEEG data, except for a comparison of the location of the electrodes relative to the statistical parametric map generated from a contrast (Fig 2a,d). It will be helpful to build a model linking between the neural responses to the voxel response in the same location - i.e., estimate from the electrophysiology data the fMRI data (e.g., Logothetis & Wandell, 2004).

As mentioned above the comparison between fMRI and SEEG is indirect (i.e., collected at different times and not related on a trial-by-trial basis for instance) and would not allow to make such a model.

(b) More comprehensive analyses of the SSVEP neural data: It will be helpful to show the results of the frequency analyses of the SSVEP data for all neurons to show that there are significant visual responses and significant face responses. It will be also useful to compare and quantify the magnitude of the face responses compared to the visual responses.

The data has been analyzed comprehensively, but we would not be able to show all neurons with such significant visual responses and face-selective responses.

(c) The neuron shown in E shows cyclical responses tied to the onset of the stimuli, is this the visual response?

Correct, it’s the visual response at 6 Hz.

If so, why is there an increase in the firing rate of the neuron before the face stimulus is shown in time 0?

Because the stimulation is continuous. What is displayed at 0 is the onset of the face stimulus, with each face stimulus being preceded by 4 images of nonface objects.

The neuron's data seems different than the average response across neurons; This raises a concern about interpreting the average response across neurons in panel F which seems different than the single neuron responses

The reviewer is correct, and we apologize for the confusion. This is because the average data on panel F has been notch-filtered for the 6 Hz (and harmonic responses), as indicated in the methods (p.11):  ‘a FFT notch filter (filter width = 0.05 Hz) was then applied on the 70 s single or multi-units time-series to remove the general visual response at 6 Hz and two additional harmonics (i.e., 12 and 18 Hz)’.

Here is the same data without the notch-filter (the 6Hz periodic response is clearly visible):

Author response image 2.

For sake of clarity, we prefer presenting the notch-filtered data in the paper, but the revised version will make it clear in the figure caption that the average data has been notch-filtered.

(d) Related to (c) it would be useful to show raster plots of all neurons and quantify if the neural responses within a region are homogeneous or heterogeneous. This would add data relating the single neuron response to the population responses measured from fMRI. See also Nir 2009.

We agree with the reviewer that this is interesting, but again we do not think that it is necessary for the point made in the present paper. Responses in these regions appear rather heterogenous, and we are currently working on a longer paper with additional SEEG data (other patients tested for shorter sessions) to define and quantify the face-selective neurons in the MidFusiform gyrus with this approach (without relating it to the fMRI contrast as reported here).

(e) When reporting group average data (e.g., Fig 2C,F) it is necessary to show standard deviation of the response across neurons.

We agree with the reviewer and have modified Figure 2 accordingly in the revised manuscript.

(f) Is it possible to estimate the latency of the neural responses to face and object images from the phase data? If so, this will add important information on the timing of neural responses in the human fusiform gyrus to face and object images.

The fast periodic paradigm to measure neural face-selectivity has been used in tens of studies since its original reports:

- in EEG: Rossion et al., 2015: https://doi.org/10.1167/15.1.18

- in SEEG: Jonas et al., 2016: https://doi.org/10.1073/pnas.1522033113

In this paradigm, the face-selective response spreads to several harmonics (1.2 Hz, 2.4 Hz, 3.6 Hz, etc.) (which are summed for quantifying the total face-selective amplitude). This is illustrated below by the averaged single units’ SNR spectra across all recording sessions for both participants.

Author response image 3.

There is no unique phase-value, each harmonic being associated with a phase-value, so that the timing cannot be unambiguously extracted from phase values. Instead, the onset latency is computed directly from the time-domain responses, which is more straightforward and reliable than using the phase. Note that the present paper is not about the specific time-courses of the different types of neurons, which would require a more comprehensive report, but which is not necessary to support the point made in the present paper about the SEEG-fMRI sign relationship.

g) Related to (e) In total the authors recorded data from 245 units (some single units and some multiunits) and they found that both in the face and nonface selective most of the recoded neurons exhibited face -selectivity, which this reader found confusing: They write “ Among all visually responsive neurons, we found a very high proportion of face-selective neurons (p < 0.05) in both activated and deactivated MidFG regions (P1: 98.1%; N = 51/52; P2: 86.6%; N = 110/127)’. Is the face selectivity in P1 an increase in response to faces and P2 a reduction in response to faces or in both it’s an increase in response to faces

Face-selectivity is defined as a DIFFERENTIAL response to faces compared to objects, not necessarily a larger response to faces. So yes, face-selectivity in P1 is an increase in response to faces and P2 a reduction in response to faces.

(1) Additional methods

(a) it is unclear if the SSVEP analyses of neural responses were done on the spikes or the raw electrical signal. If the former, how is the SSVEP frequency analysis done on discrete data like action potentials?

The FFT is applied directly on spike trains using Matlab’s discrete Fourier Transform function. This function is suitable to be applied to spike trains in the same way as to any sampled digital signal (here, the microwires signal was sampled at 30 kHz, see Methods).

In complementary analyses, we also attempted to apply the FFT on spike trains that had been temporally smoothed by convolving them with a 20ms square window (Le Cam et al., 2023, cited in the paper ). This did not change the outcome of the frequency analyses in the frequency range we are interested in.

(b) it is unclear why the onset time was shifted by 33ms; one can measure the phase of the response relative to the cycle onset and use that to estimate the delay between the onset of a stimulus and the onset of the response. Adding phase information will be useful.

The onset time was shifted by 33ms because the stimuli are presented with a sinewave contrast modulation (i.e., at 0ms, the stimulus has 0% contrast). 100% contrast is reached at half a stimulation cycle, which is 83.33ms here, but a response is likely triggered before reaching 100% contrast. To estimate the delay between the start of the sinewave (0% contrast) and the triggering of a neural response, we tested 7 SEEG participants with the same images presented in FPVS sequences either as a sinewave contrast (black line) modulation or as a squarewave (i.e. abrupt) contrast modulation (red line).  The 33ms value is based on these LFP data obtained in response to such sinewave stimulation and squarewave stimulation of the same paradigm. This delay corresponds to 4 screen refresh frames (120 Hz refresh rate = 8.33ms by frame) and 35% of the full contrast, as illustrated below (please see also Retter, T. L., & Rossion, B. (2016). Uncovering the neural magnitude and spatio-temporal dynamics of natural image categorization in a fast visual stream. Neuropsychologia, 91, 9–28).

Author response image 4.

(2) Interpretation of suppression:

The SSVEP paradigm alternates between 2 conditions: faces and objects and has no baseline; In other words, responses to faces are measured relative to the baseline response to objects so that any region that contains neurons that have a lower firing rate to faces than objects is bound to show a lower response in the SSVEP signal. Therefore, because the experiment does not have a true baseline (e.g. blank screen, with no visual stimulation) this experimental design cannot distinguish between lower firing rate to faces vs suppression of response to faces.

The strongest evidence put forward for suppression is the response of non-visual neurons that was also reduced when patients looked at faces, but since these are non-visual neurons, it is unclear how to interpret the responses to faces.

We understand this point, but how does the reviewer know that these are non-visual neurons? Because these neurons are located in the visual cortex, they are likely to be visual neurons that are not responsive to non-face objects. In any case, as the reviewer writes, we think it’s strong evidence for suppression.

We thank all three reviewers for their positive evaluation of our paper and their constructive comments.

Author response:

We thank all reviewers for the highly detailed review and the time and effort which has been invested in this review. We have read their perspectives, questions and suggested improvements with great interest. We have reflected on the public review in detail and have made the first provisional responses which are outlined below. First, we would like to respond to four main issues pointed out by the editor and reviewers:

(1) Lack of yield data in the manuscript: There have been yield data collected in most of the sites and years of our study, and these have already been published and cited in our manuscript. In the appendix of our manuscript, we included a table with yield data for the sites and years in which the beetle diversity was studied. These data show that strip cropping does not cause a systematic yield reduction.

(2) Sampling design clarification: Our paper combines data from trials conducted at different locations and years. On the one hand this allows an analysis of a comprehensive dataset, but on the other hand in some cases there were slight inconsistencies in how data were collected or processed (e.g. taxonomic level of species identification). We will explain the sampling design and data analysis in more detail to increase clarity and transparency.

(3) Additional data analysis: In the revised manuscript we will present an analysis on the responses of abundances of the 12 most common ground beetle genera to strip cropping. This will give better insight of the variation in responses among ground beetle taxa.

(4) Restrict findings to our system: We will nuance our findings further and will focus more strongly on the implications of our data on ground beetle communities, rather than on agrobiodiversity in a broader sense.

We will further work on improving the manuscript based on reviewers feedback in the coming weeks, aiming to submit a revised version of the manuscript at the end of February.

Detailed response to editor and reviewers:

Editor Comments:

(1) You only have analyzed ground beetle diversity, it would be important to add data on crop yields, which certainly must be available (note that in normal intercropping these would likely be enhanced as well).

Most yield data have been published in three previous papers, which we already cited or will cite (one was not yet published at the time of submission). Our argumentation is based on these studies. We had also already included a table in the appendix that showed the yield data that relates specifically to our locations and years of measurement. The finding that strip cropping does not majorly affect yield is based on these findings. We will consider changing the title of our manuscript to remove the explicit focus on yield.

(2) Considering the heterogeneous data involving different experiments it is particularly important to describe the sampling design in detail and explain how various hierarchical levels were accounted for in the analysis.

We agree that some important details to our analysis were not described in sufficient detail. Especially reviewer 2 pointed out several relevant points that we did account for in our analyses, but which were not clear from the text in the methods section. We are convinced that our data analyses are robust and that our conclusions are supported by the data. We will revise the methods section to make our approach clearer and more transparent.

(3) In addition to relative changes in richness and density of ground beetles you should also present the data from which these have been derived. Furthermore, you could also analyze and interpret the response of the different individual taxa to strip cropping.

With our heterogeneous dataset it was quite complicated to show overall patterns of absolute changes in ground beetle abundance and richness, especially for the field-level analyses. As the sampling design was not always the same and occasionally samples were missing, the number of year series that made up a datapoint were different among locations and years. However, we always made sure that for the comparison of a paired monoculture and strip cropping field, the number of year series was always made equal through rarefaction. That is, the number of ground beetle(s) (species) are always expressed as the number per 2 to 6 samples. Therefore, we prefer to stick to relative changes as we are convinced that this gives a fairer representation of our complex dataset.

We agree with the second point that both the editor and several reviewers pointed out. The indicator species analyses that we used were biased by rare species, and we now omit this analysis. Instead, we will include a GLM analysis on the responses of abundances of the 12 most common ground beetle genera to strip cropping. We chose for genera here (and not species) as we could then include all locations and years within the analysis, and in most cases a genus was dominated by a single species (but notable exceptions were Amara and Harpalus, which were made up of several species). We will illustrate these findings still in a similar fashion as we did for the indicator species analysis.

(4) Keep to your findings and don't overstate them but try to better connect them to basic ecological hypotheses potentially explaining them.

After careful consideration of the important points that reviewers point out, we decided to nuance our points about biodiversity conservation along two key lines: (1) the extent to which ground beetles can be indicators of wider biodiversity changes; and (2) our findings that are not as straightforward positive as our narrative suggests. We still believe that strip cropping contributes positively to carabid communities, and will carefully check the text to avoid overstatements.

Reviewer 1:

Summary:

This study demonstrates that strip cropping enhances the taxonomic diversity of ground beetles across organically-managed crop systems in the Netherlands. In particular, strip cropping supported 15% more ground beetle species and 30% more individuals compared to monocultures.

Strengths:

A well-written study with well-analyzed data of a complex design. The data could have been analyzed differently e.g. by not pooling samples, but there are pros and cons for each type of analysis and I am convinced this will not affect the main findings. A strong point is that data were collected for 4 years. This is especially strong as most data on biodiversity in cropping systems are only collected for one or two seasons. Another strong point is that several crops were included.

We thank reviewer 1 for their kind words and agree with this strength of the paper. The paper combines data from trials conducted at different locations and years. On the one hand this allows an analysis of a comprehensive dataset, but on the other hand in some cases there were slight inconsistencies in how data were collected or processed (e.g. taxonomic level of species identification).  

Weaknesses:

This study focused on the biodiversity of ground beetles and did not examine crop productivity. Therefore, I disagree with the claim that this study demonstrates biodiversity enhancement without compromising yield. The authors should present results on yield or, at the very least, provide a stronger justification for this statement.

We acknowledge that we indeed did not formally analyze yield in our study, but we have good reason for this. The claim that strip cropping does not compromise yield comes from several extensive studies (Juventia et al., 2024; Ditzler et al., 2023; Carillo-Reche et al., 2023) that were conducted in nearly all the sites and years that we included in our study. We chose not to include formal analyses of productivity for two key reasons: (1) a yield analysis would duplicate already published analyses, and (2) we prefer to focus more on the ecology of ground beetles and the effect of strip cropping on biodiversity, rather than diverging our focus also towards crop productivity. Nevertheless, we have shown the results on yield in Table S6 and refer extensively to the studies that have previously analyzed this data.

Reviewer 2:

Summary:

The authors aimed to investigate the effects of organic strip cropping on carabid richness and density as well as on crop yields. They find on average higher carabid richness and density in strip cropping and organic farming, but not in all cases.

Strengths:

Based on highly resolved species-level carabid data, the authors present estimates for many different crop types, some of them rarely studied, at the same time. The authors did a great job investigating different aspects of the assemblages (although some questions remain concerning the analyses) and they present their results in a visually pleasing and intuitive way.

We appreciate the kind words of reviewer 2 and their acknowledgement of the extensiveness of our dataset. In our opinion, the inclusion of many different crops is indeed a strength, rarely seen in similar studies; and we are happy that the figures are appreciated.

Weaknesses:

The authors used data from four different strip cropping experiments and there is no real replication in space as all of these differed in many aspects (different crops, different areas between years, different combinations, design of the strip cropping (orientation and width), sampling effort and sample sizes of beetles (differing more than 35 fold between sites; L 100f); for more differences see L 237ff). The reader gets the impression that the authors stitched data from various places together that were not made to fit together. This may not be a problem per se but it surely limits the strength of the data as results for various crops may only be based on small samples from one or two sites (it is generally unclear how many samples were used for each crop/crop combination).

The paper indeed combines data from trials conducted at different locations and years. On the one hand this allows an analysis of a comprehensive dataset, but on the other hand in some cases there were slight differences in the experimental design. At the time that we did our research, there were only a handful of farmers that were employing strip cropping within the Netherlands, which greatly reduced the number of fields for our study. Therefore, we worked in the sites that were available and studied as many crops on these sites. Since there was variation in the crops grown in the sites, for some crops we have limited replication. In the revision we will explain this more clearly.

One of my major concerns is that it is completely unclear where carabids were collected. As some strips were 3m wide, some others were 6m and the monoculture plots large, it can be expected that carabids were collected at different distances from the plot edge. This alone, however, was conclusively shown to affect carabid assemblages dramatically and could easily outweigh the differences shown here if not accounted for in the models (see e.g. Boetzl et al. (2024) or Knapp et al. (2019) among many other studies on within field-distributions of carabids).

Point well taken and we will present a more detailed description of the sampling design in the methods. Samples were always taken at least 10 meters into the field, and always in the middle of the strip. This would indeed mean that there is a small difference between the 3- and 6m wide strips regarding distance from another strip, but this was then only a difference of 1.5 to 3 meters from the edge. A difference that, based on our own extensive experience with ground beetle communities, will not have a large impact on the findings of ground beetles. The distance from field/plot edges was similar between monocultures and strip cropped fields.

The authors hint at a related but somewhat different problem in L 137ff - carabid assemblages sampled in strips were sampled in closer proximity to each other than assemblages in monoculture fields which is very likely a problem. The authors did not check whether their results are spatially autocorrelated and this shortcoming is hard to account for as it would have required a much bigger, spatially replicated design in which distances are maintained from the beginning. This limitation needs to be stated more clearly in the manuscript.

This is a limitation that is hard to avoid in comparisons between strip cropping and monoculture systems because the use of a statistically robust design with sufficient replication and still using field sizes that are representative for farming practice are often not possible. We will acknowledge this limitation in the revised manuscript. To allow a fair comparison based on sufficient number of replications, we chose to combine data from several years and locations (despite this not being the ideal experimental design). This approach has the drawback that ground beetle communities are difficult to compare. Therefore, we chose to further investigate two years of data from Wageningen as the factorial design allowed a fair comparison between monocultures and strip cropping. We analyzed three crop combinations during two years, but we still cannot exclude a potential influence of spatial autocorrelation. We acknowledged this limitation in our original submission, and we will clarify this point further in the revision. 

Similarly, we know that carabid richness and density depend strongly on crop type (see e.g. Toivonen et al. (2022)) which could have biased results if the design is not balanced (this information is missing but it seems to be the case, see e.g. Celeriac in Almere in 2022).

The samples size ranges between 2 and 6 per combination of cropping design, crop, location and year. We believe that this will allow a meaningful analysis. Moreover, our main focus is the comparison between monoculture and strip cropping, and not the comparison between different crops. Even though we show that crop types have different ground beetle communities, we are most interested in the contrast of ground beetle communities in strip cropping and monoculture systems.  

A more basic problem is that the reader neither learns where traps were located, how missing traps were treated for analyses how many samples there were per crop or crop combination (in a simple way, not through Table S7 - there has to have been a logic in each of these field trials) or why there are differences in the number of samples from the same location and year (see Table S7). This information needs to be added to the methods section.

Point well taken. We will clarify this further in the revised manuscript. As we combined data from several experimental designs that originally had slightly different research questions, this in part caused differences between numbers of rounds or samples per crop, location or year.

As carabid assemblages undergo rapid phenological changes across the year, assemblages that are collected at different phenological points within and across years cannot easily be compared. The authors would need to standardize for this and make sure that the assemblages they analyze are comparable prior to analyses. Otherwise, I see the possibility that the reported differences might simply be biased by phenology.

We agree and we dealt with this issue by using year series instead of using individual samples of different rounds. While this approach is not perfect, it allows us to get the best possible impression of the entire ground beetle community across seasons. For our analyses we had the choice to only include data from sampling rounds that were conducted at the same time, or to include all available data. We chose to analyze all data, and made sure that the number of samples between strip cropping and monoculture fields per location, year and crop was always the same by pooling and rarefaction. In this way we have analyzed a complex multi-year, multi-crop and multi-location dataset as good as we could.

Surrounding landscape structure is known to affect carabid richness and density and could thus also bias observed differences between treatments at the same locations (lower overall richness => lower differences between treatments). Landscape structure has not been taken into account in any way.

We did not include landscape structure as there are only 4 sites, which does not allow a meaningful analysis of potential effects landscape structure. Studying how landscape interacts with strip cropping to influence insect biodiversity would require at least, say 15 to 20 sites, which was not feasible for this study. However, such an analysis may be possible in an ongoing project (CropMix) which includes many farms that work with strip cropping.

In the statistical analyses, it is unclear whether the authors used estimated marginal means (as they should) - this needs to be clarified.

In the revised manuscript we will further clarify this point.

In addition, and as mentioned by Dr. Rasmann in the previous round (comment 1), the manuscript, in its current form, still suffers from simplified generalizations that 'oversell' the impact of the study and should be avoided. The authors restricted their analyses to ground beetles and based their conclusions on a design with many 'heterogeneities' - they should not draw conclusions for farmland biodiversity but stick to their system and report what they found. Although I understand the authors have previously stated that this is 'not practically feasible', the reason for this comment is simply to say that the authors should not oversell their findings.

In the revised manuscript, we will nuance our findings by explaining that strip cropping is a potentially useful tool to support ground beetle biodiversity in agricultural fields, but the effects on other taxa still needs to be further explored.

Reviewer 3:

Summary:

In this paper, the authors made a sincere effort to show the effects of strip cropping, a technique of alternating crops in small strips of several meters wide, on ground beetle diversity. They state that strip cropping can be a useful tool for bending the curve of biodiversity loss in agricultural systems as strip cropping shows a relative increase in species diversity (i.e. abundance and species richness) of the ground beetle communities compared to monocultures. Moreover, strip cropping has the added advantage of not having to compromise on agricultural yields.

Strengths:

The article is well written; it has an easily readable tone of voice without too much jargon or overly complicated sentence structure. Moreover, as far as reviewing the models in depth without raw data and R scripts allows, the statistical work done by the authors looks good. They have well thought out how to handle heterogenous, yet spatially and temporarily correlated field data. The models applied and the model checks performed are appropriate for the data at hand. Combining RDA and PCA axes together is a nice touch.

We thank reviewer 3 for their kind words and appreciation for the simple language and analysis that we used.

Weaknesses:

The evidence for strip cropping bringing added value for biodiversity is mixed at best. Yes, there is an increase in relative abundance and species richness at the field level, but it is not convincingly shown this difference is robust or can be linked to clear structural and hypothesised advantages of the strip cropping system. The same results could have been used to conclude that there are only very limited signs of real added value of strip cropping compared to monocultures.

Point well taken. We agree that the effect of strip cropping on carabid beetle communities are subtle and we will nuance the text in the revised version to reflect this.

There are a number of reasons for this:

(1) Significant differences disappear at crop level, as the authors themselves clearly acknowledge, meaning that there are no differences between pairs of similar crops in the strip cropping fields and their respective monoculture. This would mean the strips effectively function as "mini-monocultures".

This is indeed in line with our conclusions. Based on our data and results, the advantages of strip cropping seem mostly to occur because crops with different communities are now on a same field, rather than that within the strips you get mixtures of communities related to different crops. We discussed this in the first paragraph of the discussion in the original submission.

The significant relative differences at the field level could be an artifact of aggregation instead of structural differences between strip cropping and monocultures; with enough data points things tend to get significant despite large variance. This should have been elaborated further upon by the authors with additional analyses, designed to find out where differences originate and what it tells about the functioning of the system. Or it should have provided ample reason for cautioning in drawing conclusions about the supposed effectiveness of strip cropping based on these findings.

We believe that this is a misunderstanding of our approach. In the field-level analyses we pooled samples from the same field (i.e. pseudo-replicates were pooled), resulting in a relatively small sample size of 50 samples. We will explain this better in the methods section. Therefore, the statement “with enough data points things tend to get significant” is not applicable here.

(2) The authors report percentages calculated as relative change of species richness and abundance in strip cropping compared to monocultures after rarefaction. This is in itself correct, however, it can be rather tricky to interpret because the perspective on actual species richness and abundance in the fields and treatments is completely lost; the reported percentages are dimensionless. The authors could have provided the average cumulative number of species and abundance after rarefaction. Also, range and/or standard error would have been useful to provide information as to the scale of differences between treatments. This could provide a new perspective on the magnitude of differences between the two treatments which a dimensionless percentage cannot.

We agree that this would be the preferred approach if we would have had a perfectly balanced dataset. However, this approach is not feasible with our unbalanced design and differences in sampling effort. While we acknowledge the limitation of the interpretation of percentages, it does allow reporting relative changes for each combination of location, year and crop. The number of samples on which the percentages were based were always kept equal (through rarefaction) between the cropping systems (for each combination of location, year and crop), but not among crops, years and location. The reason for this is that we did not always have an equal number of samples available between both cropping systems, and this approach allowed us to make a better estimation whenever more samples were available. For example, sometimes we had 2 samples from a strip cropped field and 6 from the monoculture, here we would use rarefaction up to 2 samples (where we would just have a better estimation from the monoculture). In other cases, we had 4 samples in both strip cropped and monoculture field, here we chose to use rarefaction to 4 samples to get a better estimation altogether. Adding a value for actual richness or abundance to the figures would have distorted these findings, as the variation would be huge (as it would represent the number of ground beetle(s) species per 2 to 6 pitfall samples). Furthermore, the dimension that reviewer 3 describes would thus be “The number of ground beetle species / individuals per 2 to 6 samples”, not a very informative unit either. We chose to trade-off better estimations of difference between cropping systems over a more readily interpretable unit.

(3) The authors appear to not have modelled the abundance of any of the dominant ground beetle species themselves. Therefore it becomes impossible to assess which important species are responsible (if any) for the differences found in activity density between strip cropping and monocultures and the possible life history traits related reasons for the differences, or lack thereof, that are found. A big advantage of using ground beetles is that many life history traits are well studied and these should be used whenever there is reason, as there clearly is in this case. Moreover, it is unclear which species are responsible for the difference in species richness found at the field level. Are these dominant species or singletons? Do the strip cropping fields contain species that are absent in the monoculture fields and are not the cause of random variation or sampling? Unfortunately, the authors do not report on any of these details of the communities that were found, which makes the results much less robust.

Thank you for raising this point. We have reconsidered our indicator species analysis and found that it is rather sensitive for rare species and insensitive for changes in common species. Therefore, we will replace the indicator species analyses with a GLM analysis for the 12 most common genera of ground beetles In the revised manuscript. This will allow us to go more in depth on specific traits of the genera which abundances change depending on the cropping system. In the revised manuscript, we will also discuss these common genera more in depth, rather than focusing on rarer species. Furthermore, we will add information on rarity and habitat preference to the table that shows species abundances per location (Table S2).

(4) In the discussion they conclude that there is only a limited amount of interstrip movement by ground beetles. Otherwise, the results of the crop-level statistical tests would have shown significant deviation from corresponding monocultures. This is a clear indication that the strips function more like mini-monocultures instead of being more than the sum of its parts.

This is in line with our point in the first paragraph of the discussion and an important message of our manuscript.

(5) The RDA results show a modelled variable of differences in community composition between strip cropping and monoculture. Percentages of explained variation of the first RDA axis are extremely low, and even then, the effect of location and/or year appear to peak through (Figure S3), even though these are not part of the modelling. Moreover, there is no indication of clustering of strip cropping on the RDA axis, or in fact on the first principal component axis in the larger RDA models. This means the explanatory power of different treatments is also extremely low. The crop level RDA's show some clustering, but hardly any consistent pattern in either communities of crops or species correlations, indicating that differences between strip cropping and monocultures are very small.

We agree and we make a similar point in the first paragraph of the discussion.

Furthermore, there are a number of additional weaknesses in the paper that should be addressed:

The introduction lacks focus on the issues at hand. Too much space is taken up by facts on insect decline and land sharing vs. land sparing and not enough attention is spent on the scientific discussion underlying the statements made about crop diversification as a restoration strategy. They are simply stated as facts or as hypotheses with many references that are not mentioned or linked to in the text. An explicit link to the results found in the large number of references should be provided.

We will streamline the introduction by omitting the land sharing vs. land sparing topic and better linking references to our research findings.

The mechanistic understanding of strip cropping is what is at stake here. Does strip cropping behave similarly to intercropping, a technique that has been proven to be beneficial to biodiversity because of added effects due to increased resource efficiency and greater plant species richness? This should be the main testing point and agenda of strip cropping. Do the biodiversity benefits that have been shown for intercropping also work in strip cropping fields? The ground beetles are one way to test this. Hypotheses should originate from this and should be stated clearly and mechanistically.

We agree with the reviewer and will clarify this research direction clearer in the introduction of the revised manuscript.

One could question how useful indicator species analysis (ISA) is for a study in which predominantly highly eurytopic species are found. These are by definition uncritical of their habitat. Is there any mechanistic hypothesis underlying a suspected difference to be found in preferences for either strip cropping or monocultures of the species that were expected to be caught? In other words, did the authors have any a priori reasons to suspect differences, or has this been an exploratory exercise from which unexplained significant results should be used with great caution?

Point well taken. We agree that the indicator species analysis has limitations and therefore now replaced this with GLM analysis for the 12 most common ground beetle genera.

However, setting these objections aside there are in fact significant results with strong species associations both with monocultures and strip cropping. Unfortunately, the authors do not dig deeper into the patterns found a posteriori either. Why would some species associate so strongly with strip cropping? Do these species show a pattern of pitfall catches that deviate from other species, in that they are found in a wide range of strips with different crops in one strip cropping field and therefore may benefit from an increased abundance of food or shelter? Also, why would so many species associate with monocultures? Is this in any way logical? Could it be an artifact of the data instead of a meaningful pattern? Unfortunately, the authors do not progress along these lines in the methods and discussion at all.

We thank reviewer 3 for these valuable perspectives. In the revised manuscript, we will further explore the species/genera that respond to cropping systems and discuss these findings in more detail.

A second question raised in the introduction is whether the arable fields that form part of this study contain rare species. Unfortunately, the authors do not elaborate further on this. Do they expect rare species to be more prevalent in the strip cropping fields? Why? Has it been shown elsewhere that intercropping provides room for additional rare species?

The answer is simply no, we did not find more rare species in strip cropping. In the revised manuscript, we will add a column for rarity (according to waarneming.nl) in the table showing abundances of species per location. We only found two rare species, one of which we only found a single individual and one that was more related to the open habitat created by a failed wheat field. We will discuss this more in depth in the discussion.

Considering the implications the results of this research can have on the wider discussion of bending the curve and the effects of agroecological measures, bold claims should be made with extreme restraint and be based on extensive proof and robust findings. I am not convinced by the evidence provided in this article that the claim made by the authors that strip cropping is a useful tool for bending the curve of biodiversity loss is warranted.

We believe that strip cropping can be a useful tool because farmers readily adopt it and it can result in modest biodiversity gains without yield loss. However, strip cropping is indeed not a silver bullet (which we also don’t claim). We will nuance the implications of our study in the revised manuscript.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

Goal: Find downstream targets of cmk-1 phosphorylation, identify one that also seems to act in thermosensory habituation, test for genetic interactions between cmk-1 and this gene, and assess where these genes are acting in the thermosensory circuit during thermosensory habituation.

Methods: Two in vitro analyses of cmk-1 phosphorylation of C. elegans proteins. Thermosensory habituation of cmk-1 and tax-6 mutants and double mutants was assessed by measuring the rate of heat-evoked reversals (reversal probability) of C. elegans before and after 20s ISI repeated heat pulses over 60 minutes.

Conclusions: cmk-1 and tax-6 act in separate habituation processes, primarily in AFD, that interact complexly, but both serve to habituate the thermosensory reversal response. They found that cmk-1 primarily acts in AFD and tax-6 primarily acts in RIM (and FLP for naïve responses). They also identified hundreds of potential cmk-1 phosphorylation substrates in vitro.

Strengths:

The effect size in the genetic data is quite strong and a large number of genetic interaction experiments between cmk-1 and tax-1 demonstrate a complex interaction.

Thanks a lot for these positive remarks.

Weaknesses:

The major concern about this manuscript is the assumption that the process they are observing is habituation. The two previously cited papers using this (or a very similar) protocol, Lia and Glauser 2020 and Jordan and Glauser 2023, both use the word 'adaptation' to describe the observed behavioral decrement. Jordan and Glauser 2023 use the words 'habituation' or 'habituation-like' 10 times, however, they use 'adaptation' over 100 times. It is critical to distinguish habituation from sensory adaptation (or fatigue) in this thermal reversal protocol. These processes are often confused/conflated, however, they are very different; sensory adaptation is a process that decreases how much the nervous system is activated by a repeated stimulus, therefore it can even occur outside of the nervous system. Habituation is a learning process where the nervous system responds less to a repeated stimulus, despite (at least part of the nervous system) the nervous system still being similarly activated by the stimulus. Habituation is considered an attentional process, while adaptation is due to the fatigue of sensory transduction machinery. Control experiments such as tests for dishabituation (where the application of a different stimulus causes recovery of the decremented response) or rate of spontaneous recovery (more rapid recovery after short inter-stimulus intervals) are required to determine if habituation or sensory adaptation are occurring. These experiments will allow the results to be interpreted with clarity, without them, it isn't actually clear what biological process is actually being studied.

Thanks for the comment. As this reviewer points out, “adaptation” and “habituation” are often conflated. Many scientists (maybe not the majority though) use a less stringent definition for the word habituation, than the one presented by this reviewer. More particularly, the term habituation is used in human pain research to refer solely to the reduction of response to repeated stimuli, in the absence of a detailed assessment of the more stringent criteria mentioned here. In addition to the practice in pain research, the main reason why we steered toward ‘habituation’ from our previous publication is because it immediately conveys the idea of a response reduction, whereas ‘adaptation’ could in principle be either an up-regulation or a down-regulation of the response (again, based on various definitions). But we agree that using the word “habituation” came at the cost of triggering a confusion about the exact nature of the process, for those considering the stricter definition of the word “habituation”. In the manuscript under revision, we are changing this terminology to “adaptation”. Also following suggestions from Reviewer 2, we are strengthening the description of the protocol in the Result section and clarifying, why the adaptation phenomenon is not a ‘thermal damage’ effect or ‘fatigue’ effect in the neuro-muscular circuit controlling reversal.

While the discrepancy between the in vitro phosphorylation experiments and the in silico predictions was discussed, the substantial discrepancy (over 85% of the substrates in the smaller in vitro dataset were not identified in the larger dataset) between the two different in vitro datasets was not discussed. This is surprising, as these approaches were quite similar, and it may indicate a measure of unreliability in the in vitro datasets (or high false negative rates).

Thanks for the comment. This is an important aspect which we will more extensively cover in the Discussion section of the revised manuscript.

The strong consistency of the CMK-1 recognition consensus sequences across the two in vitro dataset speaks against the unreliability of the analyses. Instead, there are a few points to highlight that explain the somewhat low degree of overlap between the two datasets, which indeed relate to the false negative rates as this reviewer suggests.

(1) In the peptide library analysis, Trypsin cleavage prior to kinase treatment will leave a charged N-term or C- terminus and in addition remove part of the protein context required for efficient kinase recognition. This will have a variable effect across the different substrates in the peptide library, depending on the distance between the cleavage site and the phosphosite, but will not affect the native protein library. This effect increases the false negative rate in the peptide library.

(2) The number and distribution of “available substrate phosphosites” diverge in the two libraries. Indeed, the peptide library is expected to contain a markedly larger diversity of potential CMK-1 substrate sites than the protein library (because the Trypsin digestion will reveal substrates that are normally buried in a native protein), but the depth of MS analysis is the same for the two libraries. In somewhat simplistic terms, the peptide-library analysis is prone to be saturated with abundant phosphorylated peptides, which prevent detecting all phosphosites. If the peptide analysis could have been made deeper, we would probably have increased the overlap (at the cost of increasing the number of false positive too).

(3) We have chosen quite strict criteria and applied them separately to define each hit list; therefore, we know we have many false negatives in each list, which will naturally reduce the expected overlap.

As we will clarify in the revised manuscript, we tend to give more trust to the protein-library dataset (since substrates are in a configuration closer to that in vivo), with those hits also present in the peptide dataset (like TAX-6 was) as the most convincing hits, as they could be validated in a second type of experiment.

Additionally, the rationale for, and distinction between, the two separate in vitro experiments is not made clear.

We reasoned that both substrate types have their own benefits and limitations (as discussed in the manuscript), so it was an added value to run both. We proposed that the subset of targets present in both datasets to be the most solid list of candidates. We will also reinforce our point in the revised discussion that the protein-library is likely to contain much less false positives.

Line 207: After reporting that both tax-6 and cnb-1 mutants have high spontaneous reversals, it is not made clear why cnb-1 is not further explored in the paper. Additionally, this spontaneous reversal data should be in a supplementary figure.

We kept the focus of the article primarily on TAX-6, because it was identified as CMK-1 target in vitro; CNB-1 was not. Moreover, we didn’t have cnb-1(gf) mutants to pursue the analysis, and we were stuck by the cnb-1(lf) constitutive high reversal rate for any further follow up. We have added a supplementary file to present the spontaneous reversals rates.

Figure 3 -S1: This model doesn't explain why the cmk-1(gf) group and the cmk-1(gf) +cyclo A group cause enhanced response decrement (presumably by reducing the inhibition by tax-6) but the +cyclo A group (inhibited tax-6) showed weaker response decrement, as here there is even further weakened inhibition of tax-6 on this process. Also, the cmk-1(lf) +cyclo A group is labeled as constitutive habituation, however, this doesn't appear to be the case in Figure 3 (seems like a similar initial level and response decrement phenotype to wildtype).

Thanks a lot for the comment. We are glad that the presentation of our complex dataset was clear enough to bring the reader to that level of detailed reflection and interpretation on the proposed model. To address the two points raised in this reviewer’s comment, we are modifying to the model presentation and provide additional clarifications below, where we use the term adaptation instead of habituation (as in the revised Figure):

Regarding the first point, “why the cmk-1(gf) group and the cmk-1(gf) +cyclo A group cause enhanced response decrement … but the +cyclo A group showed weaker response decrement”. This is really a very good point, that cannot be easily explained if all the branches (arrows) in the model have the same weight or work as ON/OFF switches. We tried to convey the relative importance of the regulation effect via the thickness of the arrow lines (which we will clarified in the legend in the revised ms). The main ‘quantitative’ nuances to take into consideration here originate from 2 assuption of the model (which we are clarifying in the revised  manuscript):

Assumption 1: the inhibitory effect of TAX-6 on the CMK-1 anti-adaptation branch and the inhibitory effect of TAX-6 on the CMK-1 pro-adaptation branch are not of the same magnitude (we have further enhanced the line thickness differences in the revised model, top left panel for wild type).

Assumption 2: the two antagonistic direct effects of CMK-1 on adaptation are not of the same magnitude, most strikingly in the context of CMK-1(gf) mutants.

In our model, the cyclosporin A treatment alone (bottom left panel) causes a strong boost on the CMK-1 inhibitory branch and a less marked boost on the CMK-1 activator branch (following assumption 1). This causes an imbalance between the two antagonist direct CMK-1-dependent drives, which reduces (but doesn’t fully block) adaptation. Indeed, we don’t observe a total block of adaptation with cyclosporin A in wild type, the effect being significantly milder than the totally non-adapting phenotypes seen, e.g., in TAX-6(gf) mutants. From there, the question is what happen in CMK-1(gf) background that would mask the anti-adaptation effect of Cyclosporin A? Here assumption 2 is relevant, and the CMK-1(gf) pro-adaptation direct branch is always prevalent and imbalance the regulation toward faster adaptation (the role of TAX-6 becoming negligible in the CMK-1(gf) background and ipso facto that of Cyclosporin A).

Regarding the second point, “the cmk-1(lf) +cyclo A group is labeled as constitutive habituation”. We regret a confusing word choice in the first version of the manuscript; we intended to mean “normal habituation phenotype” but in the joint absence of antagonistic CMK-1 and TAX-6 regulatory signaling (so the regulation is not like in wild-type, but the phenotype ends up like in wild type). We are modifying the label to “normal adaptation” and will leave a note in the legend that an apparently normal adaptation phenotype seems to be the “default” situation when the two antagonistic regulatory pathways are shut off.

More discussion of the significance of the sites of cmk-1 and tax-6 function in the neural circuit should take place. Additionally, incorporating the suspected loci of cmk-1 and tax-6 in the neural circuit into the model would be interesting (using proper hypothetical language). For example, as it seems like AFD is not required for the naïve reversal response but just its reduction, cmk-1 activity in AFD might be generating inhibition of the reversal response by AFD. It certainly would be understandable if this isn't workable, given extrasynaptic signaling and other unknowns, but it potentially could also be helpful in generating a working model for these complex interactions. For example, cmk-1 induces AIZ inhibition of AVA (AIZ is electrically coupled to AFD), and tax-6 reduces RIM activation of AVA (these neurons are also electrically coupled according to the diagram). RIM is also a neuropeptide-rich neuron, so this could allow it to interact with the cmk-1-related process(es) in AFD. Some discussion of possibilities like this could be informative.

Thanks for the comment. These hypothetical inter-cellular communication pathways are indeed nice possibilities. On the other hand, we could envision several additional pathways. Following this helpful suggestion, we will expand the discussion of hypothetical models in the revised manuscript-

Provide an explanation for why some of the experiments in Figure 4 have such a high N, compared to other experiments.

The conditions with the highest n correspond to conditions which we have also used as ‘control’ condition for other type of experiments in the lab and as part of side projects, but which could be gathered for the present article. We have been working with cmk-1(lf) and tax-6(gf) mutants for many years… and the robust non-adapting phenotype was a reference point and a quality control when analyzing other non-adapting mutants.

Because the loss of function and gain of function mutations in cmk-1 have a similar effect, it is likely that this thermosensory plasticity phenotype is sensitive to levels of cmk-1 activity. Therefore, it is not surprising that the cmk-1 promoter failed to rescue very well as these plasmid-driven rescues often result in overexpression. Given this and that the cmk-1p rescue itself was so modest, these rescue experiments are not entirely convincing (and very hard to interpret; for example, is the AFD rescue or the ASER rescue more complete? The ASER one is actually closer to the cmk-1p rescue). Given the sensitivity to cmk-1 activity levels, a degradation strategy would be more likely to deliver clear results (or perhaps even the overactivation approach used for tax-6).

Thanks for the comment. We respectfully disagree with this reviewer’s statement “the loss of function and gain of function mutations in cmk-1 have a similar effect”. We suspect a confusion here, because our data clearly show that these two mutant types have an opposite phenotype. That being said, we interpret the weak rescue effect with cmk-1p as a probable result of overexpression or incomplete/imbalanced expression across neurons (as the promoter used might not include all the relevant regulatory regions). We dedicated considerable efforts to establish an endogenous CMK-1::degron knock in, for tissue-specific auxin-induced degradation (AID), but we were unfortunately not able to obtain consistent results. Unfortunately, the only useful data regarding CMK-1 place-of-action are the cell-specific rescue data already included in the report.

Reviewer #2 (Public review):

Summary:

The reduction in a response to a specific stimulus after repeated exposures is called habituation. Alterations in habituation to noxious stimuli are associated with chronic pain in humans, however, the underlying molecular mechanisms involved are not clear. This study uses the nematode C. elegans to study genes and mechanisms that underlie habituation to a form of noxious stimuli based on heat, termed thermo-noxious stimuli. The authors previously showed that the Calcium/Calmodulin-dependent protein kinase (CMK-1) regulates thermo-nociceptive habituation in the nematode C. elegans. Although CMK-1 is a kinase with many known substrates, the downstream targets relevant for thermo-nociceptive habituation are not known. In this study, the authors use two different kinase screens to identify phosphorylation targets of CMK-1. One of the targets they identify is Calcineurin (TAX-6). The authors show that CMK-1 phosphorylates a regulatory domain of Calcineurin at a highly conserved site (S443). In a series of elegant experiments, the authors use genetic and pharmacological approaches to increase or decrease CMK-1 and Calcineurin signaling to study their effects on thermo-nociceptive habituation in C. elegans. They also combine these various approaches to study the interactions between these two signaling proteins. The authors use specific promoters to determine in which neurons CMK-1 and Calcineurin function to regulate thermo-nociceptive habituation. The authors propose a model based on their findings illustrating that CMK-1 and Calcineurin act mostly in different neurons to antagonistically regulate habituation to thermo-nociceptive stimuli in a complex manner.

Strengths:

(1) Given the conservation of habituation across phylogeny, identifying genes and mechanisms that underlie nociceptive habituation in C. elegans may be relevant for understanding chronic pain in humans.

(2) The identification of canonical CaM Kinase phosphorylation motifs in the substrates identified in the CMK-1 substrate screen validates the screen.

(3) The use of loss and gain of function approaches to study the effects of CMK-1 and Calcineurin on thermo-nociceptive responses and habituation is elegant.

(4) The ability to determine the cellular place of action of CMK-1 and Calcineurin using neuron-specific promoters in the nematode is a clear strength of the genetic model system.

Thanks a lot for these positive remarks.

Weaknesses:

(1) The manuscript begins by identifying Calcineurin as a direct substrate of CMK-1 but ends by showing that CMK-1 and Calcineurin mostly act in different neurons to regulate nociceptive habituation which disrupts the logical flow of the manuscript.

We understand this point and we have carefully considered and (re-considered) the way to articulate the report. However, we could not present the story much differently as we would have no justification to investigate the role of TAX-6 and its interaction with CMK-1, if we would not have first identified it a phospho-target in vitro. Carefully considering this point, we found that the abstract of the first manuscript version was probably too cursory and susceptible to trigger wrong expectations among readers. We will extensively revise the abstract to clarify this point. Furthermore, we will reinforce this point in the last paragraph of the introduction.

(2) The physiological relevance of CMK-1 phosphorylation of Calcineurin is not clear.

We do agree and will explicitly discuss this aspect in the revised Discussion section, and make is also clear from the abstract on.

(3) It is not clear if Calcineurin is already a known substrate of CaM Kinases in other systems or if this finding is new.

We are not aware of any studies having shown Calcineurin is a direct target of CaM kinase I. But it was found to be substrate of CaM kinase II as well as of other kinases, as we explicitly presented in the discussion section. We will complement the text mentioning we are not aware of Calcineurin having so far been reported to by a CaM kinase I substrate.

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

The paper by Lee and Ouellette explores the role of cyclic-d-AMP in chlamydial developmental progression. The manuscript uses a collection of different recombinant plasmids to up- and down-regulate cdAMP production, and then uses classical molecular and microbiological approaches to examine the effects of expression induction in each of the transformed strains.

Strengths:

This laboratory is a leader in the use of molecular genetic manipulation in Chlamydia trachomatis and their efforts to make such efforts mainstream is commendable. Overall, the model described and defended by these investigators is thorough and significant.

Weaknesses:

The biggest weakness in the document is their reliance on quantitative data that is statistically not significant, in the interpretation of results. These challenges can be addressed in a revision by the authors.

Thank you for these comments. We have generated new data, which we hope the reviewer will find more compelling. These will be included in a revised manuscript.

Reviewer #2 (Public review):

Summary:

This manuscript describes the role of the production of c-di-AMP on the chlamydial developmental cycle. Chlamydia are obligate intracellular bacterial pathogens that rely on eukaryotic host cells for growth. The chlamydial life cycle depends on a cell form developmental cycle that produces phenotypically distinct cell forms with specific roles during the infectious cycle. The RB cell form replicates amplifying chlamydia numbers while the EB cell form mediates entry into new host cells disseminating the infection to new hosts. Regulation of cell form development is a critical question in chlamydia biology and pathogenesis. Chlamydia must balance amplification (RB numbers) and dissemination (EB numbers) to maximize survival in its infection niche. The main findings In this manuscript show that overexpression of the dacA-ybbR operon results in increased production of c-di-AMP and early expression of the transitionary gene hctA and late gene omcB. The authors also knocked down the expression of the dacA-ybbR operon and reported a reduction in the expression of both hctA and omcB. The authors conclude with a model suggesting the amount of c-di-AMP determines the fate of the RB, continued replication, or EB conversion. Overall, this is a very intriguing study with important implications however the data is very preliminary and the model is very rudimentary and is not well supported by the data.

Thank you for your comments. Chlamydia is not an easy experimental system, but we will do our best to address the reviewer’s concerns in a revised submission.

Describing the significance of the findings:

The findings are important and point to very exciting new avenues to explore the important questions in chlamydial cell form development. The authors present a model that is not quantified and does not match the data well.

Describing the strength of evidence:

The evidence presented is incomplete. The authors do a nice job of showing that overexpression of the dacA-ybbR operon increases c-di-AMP and that knockdown or overexpression of the catalytically dead DacA protein decreases the c-di-AMP levels. However, the effects on the developmental cycle and how they fit the proposed model are less well supported.

dacA-ybbR ectopic expression:

For the dacA-ybbR ectopic expression experiments they show that hctA is induced early but there is no significant change in OmcB gene expression. This is problematic as when RBs are treated with Pen (this paper) and (DOI 10.1128/MSYSTEMS.00689-20) hctA is expressed in the aberrant cell forms but these forms do not go on to express the late genes suggesting stress events can result in changes in the developmental expression kinetic profile. The RNA-seq data are a little reassuring as many of the EB/Late genes were shown to be upregulated by dacA-ybbR ectopic expression in this assay.

As the reviewer notes, we also generated RNAseq data, which validates that late gene transcripts (including sigma28 and sigma54 regulated genes) are statistically significantly increased earlier in the developmental cycle in parallel to increased c-di-AMP levels. The lack of statistical significance in the RT-qPCR data for omcB, which shows a trend of higher transcripts, is less concerning given the statistically significantly RNAseq dataset. We have reported the data from three replicates for the RT-qPCR and do not think it would be worthwhile to attempt more replicates in an attempt to “achieve” statistical significance.

The authors also demonstrate that this ectopic expression reduces the overall growth rate but produces EBs earlier in the cycle but overall fewer EBs late in the cycle. This observation matches their model well as when RBs convert early there is less amplification of cell numbers.

dacA knockdown and dacA(mut)

The authors showed that dacA knockdown and ectopic expression of the dacA mutant both reduced the amount of c-di-AMP. The authors show that for both of these conditions, hctA and omcB expression is reduced at 24 hpi. This was also partially supported by the RNA-seq data for the dacA knockdown as many of the late genes were downregulated. However, a shift to an increase in RB-only genes was not readily evident. This is maybe not surprising as the chlamydial inclusion would just have an increase in RB forms and changes in cell form ratios would need more time points.

Thank you for this comment. We agree that it is not surprising given the shift in cell forms. The reduction in hctA transcripts argues against a stress state as noted above by the reviewer, and the RNAseq data from dacA-KD conditions indicates at least that secondary differentiation has been delayed. We will try to clarify this in a revision.

Interestingly, the overall growth rate appears to differ in these two conditions, growth is unaffected by dacA knockdown but is significantly affected by the expression of the mutant. In both cases, EB production is repressed. The overall model they present does not support this data well as if RBs were blocked from converting into EBs then the growth rate should increase as the RB cell form replicates while the EB cell form does not. This should shift the population to replicating cells.

We agree that it seems that perturbing c-di-AMP production, whether by knockdown or overexpressing the mutant DacA(D164N), has an overall negative impact on chlamydial growth. We have generated new data, which we think will address this. These new data will be included in a revised manuscript.

Overall this is a very intriguing finding that will require more gene expression data, phenotypic characterization of cell forms, and better quantitative models to fully interpret these findings.

Author response:

Reviewer #1 (Public review):

Summary:

In this manuscript, the authors Eapen et al. investigated the peptide inhibitors of Cdc20. They applied a rational design approach, substituting residues found in the D-box consensus sequences to better align the peptides with the Cdc20-degron interface. In the process, the authors designed and tested a series of more potent binders, including ones that contain unnatural amino acids, and verified binding modes by elucidating the Cdc-20-peptide structures. The authors further showed that these peptides can engage with Cdc20 in the cellular context, and can inhibit APC/C^Cdc20 ubiquitination activity. Finally, the authors demonstrated that these peptides could be used as portable degron motifs that drive the degradation of a fused fluorescent protein.

Strengths:

This manuscript is clear and straightforward to follow. The investigation of different peptide variations was comprehensive and well-executed. This work provided the groundwork for the development of peptide drug modalities to inhibit degradation or apply peptides as portable motifs to achieve targeted degradation. Both of which are impactful.

Weaknesses:

A few minor comments:

(1) In my opinion, more attention to the solubility issue needs to be discussed and/or tested. On page 10, what is the solubility of D2 before a modification was made? The authors mentioned that position 2 is likely solvent exposed, it is not immediately clear to me why the mutation made was from one hydrophobic residue to another. What was the level of improvement in solubility? Are there any affinity data associated with the peptide that differ with D2 only at position 2?

The reviewer is correct that we have not done any detailed solubility characterisation; we refer only to observations rather than quantitative analysis. We wrote that we reverted from Leu to Ala due to solubility - we will clarify this statement to say that that we reverted to Ala, as it was the residue present in D1, for which we observed a measurable affinity by SPR and saw a concentration-dependent response in the thermal shift analysis. We do not have any peptides or affinity data that explore single-site mutations with the parental peptide of D2. D2 is included in the paper because of its link to the consensus D-box sequence and thus was the logical path to the investigations into positions 3 and 7 that come later in the manuscript.

(2) I'm not entirely convinced that the D19 density not observed in the crystal structure was due to crystal packing. This peptide is peculiar as it also did not induce any thermal stabilization of Cdc20 in the cellular thermal shift assay. Perhaps the binding of this peptide could be investigated in more detail (i.e., NMR?) Or at least more explanation could be provided.

This section will be clarified. The lack of observed density was likely due to the relatively low affinity of D19 and also to the lack of binding of the three C-terminal residues in the crystal, and consequently it has a further reduced affinity. The current wording in the manuscript puts greater emphasis on this second aspect being a D19-specific issue, even though it applies to all four soaked peptides. The extent of peptide-induced thermal stabilisations observed by TSA and CETSA is different, with the latter experiment consistently showing smaller shifts. This observation may be due to the more complex medium (cell lysate vs. purified protein) and/or different concentrations of the proteins in solution. In the CETSA, we over-expressed a HiBiT-tagged Cdc20, which is present in addition to any endogenously expressed Cdc20. Although we did not investigate it, the near identical D-box binding sites on Cdc20 and Cdh1 would suggest that there will be cross-specificity, which could further influence the CETSA experiments.

Reviewer #2 (Public review):

Summary:

The authors took a well-characterised (partly by them), important E3 ligase, in the anaphase-promoting complex, and decided to design peptide inhibitors for it based on one of the known interacting motifs (called D-box) from its substrates. They incorporate unnatural amino acids to better occupy the interaction site, improve the binding affinity, and lay foundations for future therapeutics - maybe combining their findings with additional target sites.

Strengths:

The paper is mostly strengths - a logical progression of experiments, very well explained and carried out to a high standard. The authors use a carefully chosen variety of techniques (including X-ray crystallography, multiple binding analyses, and ubiquitination assays) to verify their findings - and they impressively achieve their goals by honing in on tight-binders.

Weaknesses:

Some things are not explained fully and it would be useful to have some clarification. Why did the authors decide to model their inhibitors on the D-box motif and not the other two SLiMs that they describe?

For completeness, in addition to the D-box we did originally construct peptides based on the ABBA and KEN-box motifs, but they did not show any shift in melting temperature of cdc20 in the thermal shift assay whereas the D-box peptides did; consequently, we focused our efforts on the D-box peptides. Moreover, there is much evidence from the literature that points to the unique importance of the D-box motif in mediating productive interactions of substrates with the APC/C (i.e. those leading to polyubiquitination & degradation). One of the clearest examples is a study by Mark Hall’s lab (described in Qin et al. 2016), which tested the degradation of 15 substrates of yeast APC/C in strains carrying alleles of Cdh1 in which the docking sites for D-box, KEN or ABBA were mutated. They observed that whereas degradation of all 15 substrates depended on D-box binding, only a subset required the KEN binding site on Cdh1 and only one required the ABBA binding site. A more recent study from David Morgan’s lab (Hartooni et al. 2022) looking at binding affinities of different degron peptides concluded that KEN motif has very low affinity for Cdc20 and is unlikely to mediate degradation of APC/C-Cdc20 substrates. Engagement of substrate with the D-box receptor is therefore the most critical event mediating APC/C activity and the interaction that needs to be blocked for most effective inhibition of substrate degradation.

What exactly do they mean when they say their 'observation is consistent with the idea that high-affinity binding at degron binding sites on APC/C, such as in the case of the yeast 'pseudo-substrate' inhibitor Acm1, acts to impede polyubiquitination of the bound protein'? It's an interesting thing to think about, and probably the paper they cite explains it more but I would like to know without having to find that other paper.

Interesting results from a number of labs (Choi et al. 2008, Enquist-Newman et al. 2008, Burton et al. 2011, Qin et al. 2019) have shown that mutation of degron SLiMs in Acm1 that weaken interaction with the APC/C have the unexpected consequence of converting Acm1 from APC/C inhibitor to APC/C substrate. A necessary conclusion of these studies is that the outcome of degron binding (i.e. whether the binder functions as substrate or inhibitor) depends on factors other than D-box affinity and that D-box affinity can counteract them. One idea is that if a binder interacts too tightly, this removes some flexibility required for the polyubiquitination process. The most recent study on this question (Qin et al.2019) specifically pins the explanation for the inhibitory function of the high affinity D-box in Acm1 on its ‘D-box Extension’ (i.e. residues 8-12) preventing interaction with APC10. In our current study, the binding affinity of peptides is measured against Cdc20. In cellular assays however, the D-box must also engage APC10 for degradation to occur. It may be that the peptide binding most strongly to the D-box pocket on Cdc20 is less able to bind to APC10 and therefore less effective in triggering APC10-dependent steps in the polyubiquitination pathway. The important Hartooni et al. paper from David Morgan’s lab confirms that even though the binding of D-box residues to APC10 is very weak on its own, it can contribute 100X increase in affinity of a peptide by adding cooperativity to the interaction of D-box with co-activator.

After further reading on this topic, we will modify the relevant piece of text from:

“However, we found the opposite effect: D2 and D3 showed increased rates of mNeon degradation compared to D1 and D19 (Fig. 8C,D). This observation is consistent with the idea that high-affinity binding at degron binding sites on APC/C, such as in the case of the yeast ‘pseudo-substrate’ inhibitor Acm1, acts to impede polyubiquitination of the bound protein (Qin et al. 2019). Indeed, there is no evidence that Hsl1, which is the highest affinity natural D-box (D1) used in our study, is degraded any more rapidly than other substrates of APC/C in yeast mitosis. As shown in Qin et al., mutation of the high affinity D-box in Acm1 converts it from inhibitor to substrate (Qin et al. 2019). Overall, our results support the conclusions that all the D-box peptides engage productively with the APC/C and that the highest affinity interactors act as inhibitors rather than functional degrons of APC/C.”

to:

“However, we found the opposite effect: D2 and D3 showed increased rates of mNeon degradation compared to D1 and D19 (Fig. 8C,D). This observation is consistent with conclusions from other studies that affinity of degron binding does not necessarily correlate with efficiency of degradation. Indeed, there is no evidence that Hsl1, which is the highest affinity natural D-box (D1) used in our study, is degraded any more rapidly than other substrates of APC/C in yeast mitosis. A number of studies of a yeast ‘pseudo-substrate’ inhibitor Acm1, have shown that mutation of the high affinity D-box in Acm1 converts it from inhibitor to substrate (Choi et al. 2008, Enquist-Newman et al. 2008, Burton et al. 2011) through a mechanism that governs recruitment of APC10 (Qin et al. 2019). Our study does not consider the contribution of APC10 to binding of our peptides to APC/C^Cdc20 complex, but since there is strong cooperativity provided by this additional interaction (Hartooni et al. 2022) we propose this as the critical factor in determining the ability of the different peptides to mediate degradation of associated mNeon.”

Re Figure 6 and the fact that we did look at peptide binding in cells, these experiments were done in unsynchronised cells, so most Cdc20 would not be bound to APC/C.

Reviewer #3 (Public review):

Summary:

Eapen and coworkers use a rational design approach to generate new peptide-inspired ligands at the D-box interface of cdc20. These new peptides serve as new starting points for blocking APC/C in the context of cancer, as well as manipulating APC/C for targeted protein degradation therapeutic approaches.

Strengths:

The characterization of new peptide-like ligands is generally solid and multifaceted, including binding assays, thermal stability enhancement in vitro and in cells, X-ray crystallography, and degradation assays.

Weaknesses:

One important finding of the study is that the strongest binders did not correlate with the fastest degradation in a cellular assay, but explanations for this behavior were not supported experimentally. Some minor issues regarding experimental replicates and details were also noted.

Interesting results from a number of labs (Choi et al. 2008, Enquist-Newman et al. 2008, Burton et al. 2011, Qin et al. 2019) have shown that mutation of degron SLiMs in Acm1 that weaken interaction with the APC/C have the unexpected consequence of converting Acm1 from APC/C inhibitor to APC/C substrate. A necessary conclusion of these studies is that the outcome of degron binding (i.e. whether the binder functions as substrate or inhibitor) depends on factors other than D-box affinity and that D-box affinity can counteract them. One idea is that if a binder interacts too tightly, this removes some flexibility required for the polyubiquitination process. The most recent study on this question (Qin et al.2019) specifically pins the explanation for the inhibitory function of the high affinity D-box in Acm1 on its ‘D-box Extension’ (i.e. residues 8-12) preventing interaction with APC10. In our current study, the binding affinity of peptides is measured against Cdc20. In cellular assays however, the D-box must also engage APC10 for degradation to occur. It may be that the peptide binding most strongly to the D-box pocket on Cdc20 is less able to bind to APC10 and therefore less effective in triggering APC10-dependent steps in the polyubiquitination pathway. The important Hartooni et al. paper from David Morgan’s lab confirms that even though the binding of D-box residues to APC10 is very weak on its own, it can contribute 100X increase in affinity of a peptide by adding cooperativity to the interaction of D-box with co-activator.

After further reading on this topic, we will modify the relevant piece of text from:

“However, we found the opposite effect: D2 and D3 showed increased rates of mNeon degradation compared to D1 and D19 (Fig. 8C,D). This observation is consistent with the idea that high-affinity binding at degron binding sites on APC/C, such as in the case of the yeast ‘pseudo-substrate’ inhibitor Acm1, acts to impede polyubiquitination of the bound protein (Qin et al. 2019). Indeed, there is no evidence that Hsl1, which is the highest affinity natural D-box (D1) used in our study, is degraded any more rapidly than other substrates of APC/C in yeast mitosis. As shown in Qin et al., mutation of the high affinity D-box in Acm1 converts it from inhibitor to substrate (Qin et al. 2019). Overall, our results support the conclusions that all the D-box peptides engage productively with the APC/C and that the highest affinity interactors act as inhibitors rather than functional degrons of APC/C.”

to:

“However, we found the opposite effect: D2 and D3 showed increased rates of mNeon degradation compared to D1 and D19 (Fig. 8C,D). This observation is consistent with conclusions from other studies that affinity of degron binding does not necessarily correlate with efficiency of degradation. Indeed, there is no evidence that Hsl1, which is the highest affinity natural D-box (D1) used in our study, is degraded any more rapidly than other substrates of APC/C in yeast mitosis. A number of studies of a yeast ‘pseudo-substrate’ inhibitor Acm1, have shown that mutation of the high affinity D-box in Acm1 converts it from inhibitor to substrate (Choi et al. 2008, Enquist-Newman et al. 2008, Burton et al. 2011) through a mechanism that governs recruitment of APC10 (Qin et al. 2019). Our study does not consider the contribution of APC10 to binding of our peptides to APC/C^Cdc20 complex, but since there is strong cooperativity provided by this additional interaction (Hartooni et al. 2022) we propose this as the critical factor in determining the ability of the different peptides to mediate degradation of associated mNeon.”

Re Figure 6 and the fact that we did look at peptide binding in cells, these experiments were done in unsynchronised cells, so most Cdc20 would not be bound to APC/C.

Author response:

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

Reviewer #1 (Public review):

In the manuscript entitled "A VgrG2b fragment cleaved by caspase-11/4 promotes Pseudomonas aeruginosa infection through suppressing the NLRP3 inflammasome", Qian et al. found an activation of the non-canonical inflammasome, but not the downstream NLRP3 inflammasome, during the infection of macrophage by P. aeruginosa, which is in sharp contrast to that by E. coli (Figure 1). In realizing that the suppression of the NLRP3 inflammasome is Caspase-11 dependent, the authors performed a screening among P. aeruginosa proteins and identified VgrG2b being a major substrate of Caspase-11 (Figure 2). Next, the authors mapped the cleavage site on VgrG2b to D883, and demonstrated that cleavage of VgrG2b by Caspase-11 is essential for the suppression of the NLRP3 inflammasome (Figure 3). Furthermore, they found that a binding between the C-terminal fragment of the cleaved VgrG2b and NLRP3 existed (Figure 4), which was then proved to block the association of NLRP3 with NEK7 (Figure 5). Finally, the authors demonstrated that blocking of VgrG2b cleavage, by either mutation of the D883 or administration of a designed peptide, effectively improved the survival rate of the P. aeruginosa-infected mice (Figure 6). This is a well-designed and executed study, with the results clearly presented and stated.

We are deeply grateful for your recognition and positive comments on our article. Thank you for your effort and dedication in reviewing our manuscript. We are honored to have the opportunity to receive feedback form professional reviewers like you.

Reviewer #2 (Public review):

Summary:

In their manuscript, Quian and colleagues identified a novel mechanism by which Pseudomonas control inflammatory responses upon inflammasome activation. They identified a caspase-11 substrate (VgrG2b) which, upon cleavage, binds and inhibits the NLRP3 to reduce the production of pro-inflammatory cytokines. This is a unique mechanism that allows for the tailoring of the innate immune response upon bacterial recognition.

Strengths:

The authors are presenting here a novel conceptual framework in host-pathogen interactions. Their work is supported by a range of approaches (biochemical, cellular immunology, microbiology, animal models), and their conclusions are supported by multiple independent evidences. The work is likely to have an important impact on the innate immunity field and host-pathogen interactions field and may guide the development of novel inhibitors.

Weaknesses:

Although quite exhaustive, a few of the authors' conclusions are not fully supported (e.g., caspase-11 directly cleaving VgrG2b, the unique affinity of VgrG2b-C for NLRP3) and would require complementary approaches to validate their findings fully. This is minimal.

We sincerely appreciate your professional review and kind appraisal on our article. These comments are really valuable and helpful for improving our manuscript. According to your suggestions, we have made some modifications and added some supplemental data to make our results more convincing. The detailed responses are listed point-by-point below.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

I really enjoyed reading your manuscript and believe this is an important conceptual advance for the innate immunity field. Your conclusions are in general well-supported, you used a range of methodologies and the quality of the presentation of the results is excellent. I have a few comments here that I hope will contribute to improving an already great piece of work:

Elements to be improved:

Line 109-110: the author claims that the release of mito DNA is required for NLRP3 activation. ' I would support this with a reference. I believe this may not be fully agreed on in the field. Cleavage of GSDMD by caspase4/11 is required, however. A few groups showed the required for K+ efflux in this context (Broz, Brough, Schroder labs).

It is a very good suggestion. Indeed, there is still controversy over this issue, and we have revised our text to make our manuscript more neutral. We have also cited these important references to help readers understand where the controversy lies.

I disagree that OMV _+ Pseudomonas is a natural way to simulate natural infection. I would argue it is even quite artificial. Pseudomonas alone should be sufficient to generate OMV without the addition of extra OMVs.

This is a good point. Before we infected BMDM cells with PAO1 stains, we had washed with PBS for at least three times to exclude the interference of contents in the LB medium. Moreover, in our experimental system, the time for co-incubation between bacteria and host cells is very limited. During this time, the amount of OMV secreted by bacteria may not reach the level of activating inflammasomes, and this concentration is also relatively low compared to the OMV concentration secreted by bacteria under physiological conditions. Therefore, we added extra OMVs to simulate the chronic infection condition in a short time.

The co-expression of caspase with VrG2b and assume the cleavage is direct. However, the work is lacking work with recombinant proteases (commercially available), which would strengthen their conclusions regarding the ability of caspase-4/11 to directly cleave the protein. Based on the recognised sequence (DXXD), I believe caspase-4/11 is not directly responsible for this. These caspases were shown to cleave caspase-3/7, which can cleave such sequence (DXXX). As caspase-4 can cleave caspase-3/7 in their lysates, I would recommend testing this hypothesis to further strengthen the authors' conclusions.

These are very good points. As data shown on Fig. 3F, we used recombinant VgrG2b and caspase-11 p22/p10 to prove the direct cleavage of caspase-11. To exclude the effect of caspase-3/7, we treated cells with inhibitors of caspase-3/7 and found that caspase-3/7 are not the executor for VgrG2b cleavage (new Fig. S3E, F).

The affinity between caspase-11 and VgrG2b-C is puzzling as one would normally expect the caspase and its substrates to quickly dissociate. Does VgrG2b-C impact the activity of caspase-4/11 upon cleavage? Can VrgG2b-C also interact with p20/p10 caspase-1? I believe the authors only tried the full-length version of caspase-1 in supplemental.

These are very good questions. We agree enzymes and substrates only have temporary interactions normally, which are not easy to catch. However, we used mutant caspase-11(C254A) inhibiting its cleavage of substrates, so that the combination of VgrG2b or VgrG2b-C with caspase-11(C254A) could be detected. This mutation is frequently used in immunoprecipitation (Wang K, Cell, 2020). We had tested the impact of VgrG2b-C on the enzyme activity of caspase-4/11, and showed that VgrG2b-C did not affect the cleavage of GSDMD by caspase-11 (Fig. 5C). We also tried the caspase-1 p20/p10, also found that they had no interaction with VgrG2b-C (new Fig. S4G).

Can more details be provided about the generation of recombinant caspase-11, VgrG2b-C, and other recombinant proteins tested?

Thanks for your suggestion, we have revised our description in the new version.

The authors assumed that VgrG2C-b does not impact other inflammasome (such as NLRC4) based on their X-gal assay. I would also confirm this with a functional assay (e.g., transfection of flagellin in macrophages).

This is a good suggestion. We have tested the impact of VgrG2b-C on NLRC4 inflammasome and found that VgrG2b-C does not affect NLRC4 activation with the transfection of flagellin (new Fig. S5K).

Often, representative experiments are shown. For Elisa, cell death assays and quantitative experiments, pooling the data would be appropriate. Appropriate statistical analysis should be conducted based on this as well.

Thanks for your suggestions. In the revised manuscript, we pooled the data of three independent experiments for our analysis of ELISA and cell death assays. We also added descriptions of statistical analysis in our revised text.

VgrG2b has been suggested to be a metalloprotease (PMID: 31577948). Is its protease activity required for the phenomenon observed?

This is a very good question. The active region of metalloprotease VgrG2b-C is aa932-941, especially the core sequence of HEXXH. Structure data also confirms that H935, E936, H939, E983 play key roles in the coordination with Zn ions (Sana TG, mBio, 2015; Wood TE, Cell reports, 2019). In our study, the cleavage of VgrG2b by caspase-4/11 depends on the recognition of tetrapeptide sequence in aa880-883. We added data showing that the cleavage of VgrG2b and the inhibition of NLRP3 inflammasome were not affected by VgrG2b enzymatic activity (new Fig. S4I-K).

What is the affinity of VgrG2b-C for NLRP3? Is it higher than NEK7? A quantitative experiment would be required to claim this.

This is a great point of view. We added the quantitative data certifying that VgrG2b-C has higher affinity with NLRP3 compared with NEK7 in the revised manuscript (326 nM VS 681 nM).

The Material and Method section is a bit light and would benefit from adding more information (e.g. cell density, microscopy details, number of cells imaged, etc).

Thanks for your suggestion. We have added more details in the Material and Method section in revised manuscript.

Author response:

We thank the reviewers for their concise and detailed summaries, and appreciate the constructive feedback on the article’s strengths and weaknesses. In response, we plan to strengthen our work in a revised version by presenting the model assumptions for the electrocyte more explicitly and further elaborate on the generalisability of the results to other cell types with different ion channels including calcium and chloride.

Experimental work is beyond the scope of our modelling-based study. However, we would like our work to serve as a framework for future experimental studies into the role of the electrogenic pump current (and its possible compensatory currents) in disease, and its role in evolution of highly specialised excitable cells (such as electrocytes).

Author response:

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

Reviewer #1:

I am satisfied with all clarifications and additional analyses performed by the authors. 

The only concern I have is about changes in running after [AM+VM] mismatches. 

The authors reported that they "found no evidence of a change in running speed or pupil diameter following [AM + VM] mismatch (Figures S5A)" (line 197). 

Nevertheless, it seems that there is a clear increase in running speed for the [AM+VM] condition (S5A). Could this be more specifically quantified? I am concerned that part of the [AM+VM] could stem from this change in running behavior. Could one factor out the running contribution? 

Please excuse, this was unintentionally omitted. We have added the quantification to Table S1 and included the results of the significance test in (Fig S2A, Fig S4A and Fig S5A). The increase in running speed upon MM presentation (0.5 – 1 s), compared to the baseline running speed in the time window preceding MM presentation (-0.5 – 0 s), was not significant in any of the tested conditions.

In the process of adding the statistics, we noticed an unfortunate inconsistency in our figures that relates to Figure S5A. The data shown in all other Figures is aligned to the onset of audiomotor mismatch. In Figure S5A, however, the data were aligned to the onset of the visuomotor mismatch. As there is a differential delay in the closed loop coupling of auditory and visual feedback of approximately 170 ms (as described in the methods), visuomotor mismatch onset is slightly before audiomotor mismatch onset. We have corrected this now in the manuscript but have done the statistical analysis for both old and new versions of the figure. In neither case do we find evidence of a running speed response.

The authors thoroughly addressed the concerns raised. In my opinion, this has substantially strengthened the manuscript, enabling much clearer interpretation of the results reported. I commend the authors for the response to review. Overall, I find the experiments elegantly designed, and the results robust, providing compelling evidence for non-hierarchical interactions across neocortical areas and more specifically for the exchange of sensorimotor prediction error signals across modalities. 

We are happy to hear!

Reviewer #2:

The incorporation of the analysis of the animal's running speed and the pupil size upon sound interruption improves the interpretation of the data. The authors can now conclude that responses to the mismatch are not due to behavioral effects. 

The issue of the relationship between mismatch responses and offset responses remains uncommented. The auditory system is sensitive to transitions, also to silence. See the work of the Linden or the Barkat labs (including the work of the first author of this manuscript) on offset responses, and also that of the Mesgarani lab (Khalighinejad et al., 2019) on responses to transitions 'to clean' (Figure 1c) in human auditory cortex. Offset responses, as the first author knows well, are modulated by intensity and stimulus length (after adaptation?). That responses to the interruption of the sound are similar in quality, if not quantity, in the closed and open loop conditions suggest that offset response might modulate the mismatch response. A mismatch response that reflects a break in predictability would presumably be less modulated by the exact details of the sensory input than an offset response. Therefore, what is the relationship between the mismatch response and the mean sound amplitude prior to the sound interruption (for example during the preceding 1 second)? And between the mismatch response and the mean firing rate over the same period? 

Finally, how do visual stimuli modulate sound responses in the absence of a mismatch? Is the multimodal response potentiation specific to a mismatch?

There are probably two points important to clarify before answering the question – just to make sure there is no semantic misunderstanding. 

(1) In the jargon of predictive processing, a prediction error is a deviation from a predictable relationship. This can be sensorimotor coupling (as in audio- and visuomotor mismatch), stimulus history (as in oddball, or sound offset responses), surround sensory input (as in endstopping response and center-surround effects in visual processing), etc. A sound offset perceived by an animal in an open loop condition is thus a negative prediction error based on stimulus history (this assumes the animal has no way to predict the time of offset – as is the case in our experiments). We are primarily interested in our work here in characterizing negative prediction errors that result from motor-related predictions – hence the comparison we use is unpredictable sound offset in closed-loop coupling vs. unpredictable sound offset in open-loop coupling. The first is a mixture of an audiomotor prediction error and a stimulus history prediction error. The second is just a stimulus history prediction error. Thus, we compare the two types of responses to isolate the component that can only be attributed to audiomotor prediction errors. 

(2) Audiomotor mismatch responses can of course be explained in a large variety of ways. For example, one could consider a sound offset a sensory stimulus. One could further assume that locomotion increases sensory responses. If so, one could explain audiomotor mismatch responses as a locomotion related gain of a sensory offset response. However, we need to further postulate that this locomotion related gain is stimulus specific, as for sound onset responses there is no detectable difference between locomotion and sitting. Thus, we are left with a model that explains audiomotor mismatch responses as a “stimulus specific locomotion gain of sensory responses”. This is correct – it is just not very satisfying, has no computational basis, and makes no useful predictions (see e.g. https://pubmed.ncbi.nlm.nih.gov/36821437/ for an extended treatise of exactly this point for visuomotor mismatch responses).

That responses to the interruption of the sound are similar in quality, if not quantity, in the closed and open loop conditions suggest that offset response might modulate the mismatch response.

Conceptually both a “sound offset” and an “audiomotor mismatch” are negative prediction errors. Could one describe the effect we see as an audiomotor mismatch modulating a sound offset? Certainly. But if the reviewer means modulate in the sense of neuromodulatory – we are not aware of a neuromodulatory responses that would be fast enough (or be strong enough to have these effects – we have looked into ACh, NA, and Ser (unpublished – no MM response)). Alternatively, they could simply add linearly (as predictive processing would predict). Given that AM mismatch responses are likely computed in auditory cortex, we see no reason to speculate that anything more complicated is happening than a linear summation of different prediction error responses. 

A mismatch response that reflects a break in predictability would presumably be less modulated by the exact details of the sensory input than an offset response. Therefore, what is the relationship between the mismatch response and the mean sound amplitude prior to the sound interruption (for example during the preceding 1 second)? And between the mismatch response and the mean firing rate over the same period? 

The reviewer’s intuition here – that mismatch responses have a lower resolution than what one thinks of as sensory responses (or sound offset responses) – is probably not warranted. Experiments that quantify the resolution of mismatch responses are relatively data intense – and to the best of our knowledge this has only been done once in the visual system for visuomotor mismatch responses (Zmarz and Keller, 2016). Here we found that visuomotor mismatch responses exhibited matched spatial (in visual space) resolution to that of visual responses. 

Regarding the suggested analyses: In a closed loop session, the sound amplitude preceding the mismatch is directly related to the running speed of the mouse. In visual cortex, the amplitude of visuomotor mismatch responses linearly scales with running speed (and consequently visual flow speed) prior to the mismatch – as predicted by predictive processing. See e.g. figure 4B in (Zmarz and Keller, 2016). We have tried this analysis for audiomotor mismatches in the previous round of reviews, but we fear we do not have sufficient data to address this question properly. If we look at how mismatch responses change as a function of locomotion speed (sound amplitude) across the entire population of neurons, we have no evidence of a systematic change (and the effects are highly variable as a function of speed bins we choose). However, just looking at the most audiomotor mismatch responsive neurons, we find a trend for increased responses with increasing running speed (Author response image 1). We analyzed the top 5% of cells that showed the strongest response to mismatch (MM) and divided the MM trials into three groups based on running speed: slow (10-20 cm/s), middle (20-30 cm/s), and fast (>30 cm/s). Given the fact that we have on average 14 mismatch events in total per neuron, the analysis when split by running speed is under-powered.  

Author response image 1.

The average response of strongest AM MM responders to AM mismatches as a function of running speed (data are from 51 cells, 11 fields of view, 6 mice).

Regarding the relationship between mismatch response and firing rate prior to mismatch, we are not sure we understand the intuition. Does the reviewer mean, the average firing rate of the mismatch neuron? Or the population mean? The first is likely uninterpretable as it is bound to be confounded by regression to the mean type artefacts. But in either case, we would have no prediction of what to expect.

Author response:

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

Reviewer #1 (Public Review):

Summary: 

The authors demonstrate that, while the loss of Ezrin increases lysosomal biogenesis and function, its presence is required for the specific endocytosis of EGFR. Upon further investigation, the authors reveal that Ezrin is a crucial intermediary protein that links EGFR to AKT, leading to the phosphorylation and inhibition of TSC. TSC is a critical negative regulator of the mTORC1 complex, which is dysregulated in various diseases, making their findings a valuable addition to multiple fields of study. Their cell signaling findings are translatable to an in vivo Medaka fish model and suggest that Ezrin may play a crucial role in retinal degeneration.

Strengths: 

Giamundo, Intartaglia, et al. utilized unbiased proteomic and transcriptomic screens in Ezrin KO cells to investigate the mechanistic function of Ezrin in lysosome and cell signaling pathways. The authors' findings are consistent with past literature demonstrating Ezrin's role in the EGFR and mTORC1 signaling pathways. They used several cell lines, small molecule inhibitors, and cellular and in vivo knockout models to validate signaling changes through biochemical and microscopy assays. Their use of multiple advanced microscopy techniques is also impressive.

We are grateful to the Editor and the Reviewers for their important and constructive comments, which amended us to improve our manuscript. We have now carried out new experiments and analyses to further support our findings.

Weaknesses: 

While the authors demonstrated activation of TSC1 (lysosomal accumulation) and inactivation of Akt (decreased phosphorylation in TSC1), as well as decreased mTORC1 signaling in Ezrin knockout cells, direct experiments showing the rescue of mTORC1 activity by AKT and TSC1 mutants are required to confirm the linear signaling pathway and establish Ezrin as a mediator of EGFR-AKTTSC1-mTORC1 signaling. Although the authors presented representative images from advanced microscopy techniques to support their claims, there is insufficient quantification of these experiments. Additionally, several immunoblots in the manuscript lack vital loading controls, such as input lanes for immunoprecipitations and loading controls for western blots.

We wish to thank the Reviewer for his/her important and constructive comments on our manuscript and to consider that our study provides new information for understanding the mechanism regulating TSC/mTORC1 pathway. We have now extensively revised the manuscript according to his/her suggestions. Indeed, to expand on the evidence demonstrating Ezrin as a mediator of EGFR-AKTTSC1-mTORC1 signaling, the revised manuscript includes quantification of all advanced microscopy images, rescue experiments demonstrating the role of Ezrin in AKT/TSC/mTORC1 molecular network, and controls for WBs and immunoprecipitations.

Reviewer #2 (Public Review):

Summary: 

The authors begin with the stated goal of gaining insight into the known repression of autophagy by Ezrin, a major membrane-actin linker that assembles signaling complexes on membranes. RNA and protein expression analysis is consistent with upregulation of lysosomal proteins in Ezrin-deficient MEFs, which the authors confirm by immunostaining and western blotting for lysosomal markers. Expression analysis also implicates EGF signaling as being altered downstream of Ezrin loss, and the authors demonstrate that Ezrin promotes relocalization of EGFR from the plasma membrane to endosomes. Ezrin loss impacts downstream MAPK/Akt/mTORC1 signaling, although the mechanistic links remain unclear. An Ezrin mutant Medaka fish line was then generated to test Ezrin's role in retinal cells, which are known to be sensitive to changes in autophagy regulation. Phenotypes in this model appear generally consistent with observations made in cultured cells, though mild overall. 

Strengths: 

Data on the impact of Ezrin-loss on relocalization of EGFR from the plasma membrane are extensive, and thoroughly demonstrate that Ezrin is required for EGFR internalization in response to EGF. 

A new Ezrin-deficient in vivo model (Medaka fish) is generated.

Strong data demonstrates that Ezrin loss suppresses Akt signaling. Ezrin loss also clearly suppresses mTORC1 signaling in cell culture, although examination of mTORC1 activity is notably missing in Ezrin-deficient fish. 

We thank the Reviewer for the recognition of our study and apologize for the insufficient evidence reported in the previous version of the manuscript. As requested by the Reviewer, we considerably expanded the number of experiments to support EZRIN/EGFR/TSC molecular network in regulating autophagy pathway in the revised manuscript. Furthermore, following the Reviewer’s comment we have expanded the interpretation of our findings in the "Discussion” section. We hope the new version of our manuscript will satisfy the Reviewer’s worries.

Weaknesses: 

LC3 is used as a readout of autophagy, however the lipidated/unlipidated LC3 ratio generally does not appear to change, thus there does not appear to be evidence that Ezrin loss is affecting autophagy in this study. 

We certainly agree with the Reviewer on the importance of this issue and apologize for the lack of clarity. Ezrin is an already widely characterized protein participating autophagy pathway. Several studies, including our previous studies, demonstrated that both silencing and pharmacological inhibition of Ezrin may promote autophagy by promoting activation of TFEB, in part through the TRPML1-calcineurin signaling pathway (Naso et al 2020; Intartaglia et al 2022; Lou et al 2024). However, a full elucidation on how Ezrin controls autophagy is still not unknown. As suggested by the Reviewer, to reinforce our data, we have now fixed this inaccuracy by better elucidating this aspect in the revised manuscript. Accordingly, we have monitored the autophagic flux and LC3 expression level following the guidelines for the use and interpretation of assays for monitoring autophagy (4th edition) by Klionsky et al. 2021. The data presented in the new Figure supplement 1 now better support the notion that depletion of Ezrin increases autophagic flux. We hope the new version of our manuscript will satisfy the Reviewer’s worries.

The conclusion is drawn that Ezrin loss suppresses EGF signaling, however this is complicated by a strong increase in phosphorylation of the p38 MAPK substrate MK2. Without additional characterization of MAPK and Erk signaling, the effect of Ezrin loss remains unclear.  Causative conclusions between effects on MAPK, Akt, and mTORC1 signaling are frequently drawn, but the data only demonstrate correlations. For example, many signaling pathways can activate mTORC1 including MAPK/Erk, thus reduced mTORC1 activity upon Ezrin-loss cannot currently be attributed to reduced Akt signaling. Similarly, other kinases can phosphorylate TSC2 at the sites examined here, so the conclusion cannot be drawn that Ezrin-loss causes a reduction in Akt-mediated TSC2 phosphorylation.

We agree with the Reviewer that this is an interesting and important question. However, we respectfully disagree with the Reviewer and feel that addressing this point by additional studies on both MAPK and ERK pathways, as the Reviewer suggests, is outside the scope of this manuscript. We therefore prefer to address these questions in future studies. However, following the Reviewer’s comment we have expanded the interpretation of our findings in the "Discussion” section. We hope the new version of our manuscript will satisfy the Reviewer’s worries.

In Figure 7, the conclusion cannot be drawn that retinal degeneration results from aberrant EGFR signaling.

We certainly agree with the Reviewer on the importance of this issue. We now fixed this inaccuracy by adding TUNEL staining that showed the retinal degeneration in Ezrin KO medaka fish. The results of these assays are described in the Results section and documented in revised Figure 7, panels H.

It is unclear why TSC1 is highlighted in the title, as there does not appear to be any specific regulation of TSC1 here. 

We modified the title accordingly

In Figure 1 the conclusion is drawn that there is an increase in lysosome number with Ezrin KO, however it does not appear that the current analysis can distinguish an increased number from increased lysosome size or activity. Similarly, conclusions about increased lysosome "biogenesis" could instead reflect decreased turnover.

Following this Reviewer’s observation, we changed the text according to his/her suggestion.

Immunoprecipitation data for a role for Ezrin as a signaling scaffold appear minimal and seem to lack important controls.

We apologize for these inaccuracies. We have now carried out new experiments to further support our findings. Moreover, all blots were changed for better exposed images. In the revised Figures the controls were showed.

In Figure 3A it seems difficult to conclude that EGFR dimerization is reduced since the whole blot, including the background between lanes, is lighter on that side.

We now fixed this inaccuracy. The blots were changed for better exposed images in revised Figure 3, panel A. and quantified

In Figure 6C specificity controls for the TSC1 and TSC2 antibodies are not included but seem necessary since their localization patterns appear very different from each other in WT cells.

We apologize because we have created some confusion. We have now emended this mistake and revised all panels in Figure 6C (now Figure 6D) for consistency between figures and text. Concerning the specificity of TSC1 and TSC2 antibodies and staining, indeed, antibodies labelling was showing the ordinary pattern from TSC in the cells as stated in Menon et al. 2014. We would like to point out that the antibodies are the same indicated in Menon et al. 2014 and our data are not only based on TSC1 and TSC2 staining but on a considerable number of in vivo and in vitro experiments in which many and different markers were used by performing several complementary approaches (i.e. immunofluorescence, western blot analysis, Omics, etc.)

Menon S, Dibble CC, Talbott G, Hoxhaj G, Valvezan AJ, Takahashi H, Cantley LC, Manning BD. Spatial control of the TSC complex integrates insulin and nutrient regulation of mTORC1 at the lysosome. Cell. 2014 Feb 13;156(4):771-85.

In Figure 7 the signaling effects in Ezrin-deficient fish are mild compared to cultured cells, and effects on mTORC1 are not examined. Further data on the retinal cell phenotypes would strengthen the conclusions.

We thank the Reviewer for his/her comment. We have now fixed this inaccuracy in the revised manuscript. We added the analysis for p4EBP1 (S65), a mTORC1 substrate Figure 7 panel D. 

In Figure 7F there appears to be more EGFR throughout the cell, so it is difficult to conclude that more EGFR at the PM in Ezrin-/- fish means reduced internalization. 

We agree with the Reviewer that it is an important question that helped us to improve the quality of the data presented. As correctly noted by the Reviewer, EGFR protein level is increased due to EZRIN deletion. This is evident in Figure 7 panel F, in line with both proteomic analysis and in vitro experiments (Figure 2I; Figure 3E; Figure 5C). We also agree that the increase of EGFR protein level could strength the background of immunofluorescence. Therefore, to better represent the EGFR membrane translocation on flat mount RPE from medaka lines, we add a highlighting box showing it in both WT and KO medaka line in the revised Figure 7 panel F.

Reviewer #3 (Public Review): 

Summary: 

In this study, the authors have attempted to demonstrate a critical role for the cytoskeletal scaffold protein Ezrin, in the upstream regulation of EGFR/AKT/MTOR signaling. They show that in the absence of Ezrin, ligand-induced EGFR trafficking and activation at the endosomes is perturbed, with decreased endosomal recruitment of the TSC complex, and a corresponding decrease in AKT/MTOR signaling. 

Strengths: 

The authors have used a combination of novel imaging techniques, as well as conventional proteomic and biochemical assays to substantiate their findings. The findings expand our understanding of the upstream regulators of the EGFR/AKT MTOR signaling and lysosomal biogenesis, appear to be conserved in multiple species, and may have important implications for the pathogenesis and treatment of diseases involving endo-lysosomal function, such as diabetes and cancer, as well as neuro-degenerative diseases like macular degeneration. Furthermore, pharmacological targeting of Ezrin could potentially be utilized in diseases with defective TFEB/TFE3 functions like LSDs. While a majority of the findings appear to support the hypotheses, there are substantial gaps in the findings that could be better addressed. Since Ezrin appears to directly regulate MTOR activity, the effects of Ezrin KO on MTOR-regulated, TFEB/TFE3 -driven lysosomal function should be explored more thoroughly. Similarly, a more convincing analysis of autophagic flux should be carried out. Additionally, many immunoblots lack key controls (Control IgG in co-IPs) and many others merit repetition to either improve upon the quality of the existing data, validate the findings using orthogonal approaches, or provide a more rigorous quantitative assessment of the findings, as highlighted in the recommendation for authors. 

We thank the Reviewer for the recognition of our study and apologize for the inaccuracies previously. We also greatly appreciate the efforts the reviewer went through with his/her support and help for the improvement of our manuscript. We considerably expanded the number of experiments to support EZRIN/EGFR/AKT network in controlling mTORC1 pathway in the revised manuscript as requested by the Reviewer. We hope the new version of our manuscript will satisfy the Reviewer’s worries.

Reviewer #1 (Recommendations for The Authors):

Major comments: 

(1) While the authors show that, in the absence of Ezrin, TSC accumulates on the lysosome and suppresses mTORC1 signaling, they should perform additional genetic experiments to strengthen their conclusions. Can they knockout or knockdown TSC1/2 in Ezrin-deficient cells to rescue mTORC1 activity? Can they mutate the lysosomal localization signal on TSC1 (TSC1Q149E/R204E/K238E) in Ezrin-deficient cells to rescue mTORC1 activity? Does constitutively active AKT (myr-AKT or AKT-E40K) restore mTORC1 activity in Ezrin-deficient cells? 

We agree with the Reviewer that it is an important concern that helped us to improve the quality of the data presented. We now provide in the revised version of Figure supplement 4F the results of pharmacological inhibition of Ezrin on MEF-TSC2 KO cells. In line with our findings, the lack of TSC2 is able to rescue mTORC1 signaling in absence of Ezrin activity. Thus, these data strongly support that Ezrin is required for TORC1pathway via TSC complex targeting.

(2) In the absence of Ezrin, TSC1 constitutively localizes on the lysosome and suppresses mTORC1. Does this suppression hold in the presence of other mTORC1-activating signals (i.e., amino acids, insulin, oxygen)? 

Following the reviewer’s suggestion we now provide this information in the revised Figure 6C, in which we showed that stimulation with insulin does not exert its activating effect on mTORC1 signaling (i.e. phosphorylation of pP70 S6 - pT389). These new data, together with the experiments on MEF TSC2 KO cells, clearly support the model by which Ezrin works as a scaffold protein connecting ATK signaling to TSC complex. The lack of Ezrin induces a disconnection between AKT and TSC complex, which is translocated on lysosomes and insensitive to inhibition of AKT signaling.

(3) In Figure 3A, the authors showed EGFR dimerization through a western blot of a crosslinking assay. However, the western blot data are unclear and do not strongly support their statement. Additionally, the authors mentioned that the dimerization is confirmed by immunofluorescence analysis, but this statement should be revised since the imaging analysis only indirectly shows the copresence of EZR and EGFR, not necessarily the dimerized EGFR. The authors should perform additional experiments to strengthen their claim or tone down their statements in the text and model figure. 

We certainly agree with the Reviewer on the importance of this issue and now we have fixed this inaccuracy in the revised manuscript. The blots of crosslinking were changed for better exposed images in revised Figure 3, panel A. Moreover, we also properly quantified signals to support our conclusion.

(4) It is interesting that Ezrin binds EGFR, AKT, and TSC as a scaffolding protein. To define the mechanisms by which Ezrin interacts with AKT, EGFR, and TSC, can the authors perform domain analyses to determine which regions of Ezrin are required for its binding with AKT, EGFR, and TSC in mediating EGFR-AKT-TSC-mTORC1 signaling? 

We thank the Reviewer for his/her comment that improves our manuscript. Conducting domain analysis in the lab would be ideal, although this seems to us a long tour de force that might be associated to several technical and experimental issues. However, in silico approaches provide a helpful alternative for generating initial hypotheses about domain-domain interactions, though they should be seen as a starting point rather than a complete solution. Recent advances in fold prediction suggest that AlphaFold3 could be used to predict dimer formation and, consequently, domain-domain interactions. However, such an approach is challenging in this case because some of the considered proteins are transmembrane, and all are prone to form multimeric complexes with multiple partners, making them poor candidates for reliable fold predictions. In fact, the predicted dimers are poorly supported, and AlphaFold3 lacks confidence in the relative positioning of interactors, limiting its interpretability. Alternatively, database mining and machine-learning methods, such as HINT, Domine, and PPIDomainMiner, provide more robust evidence. Indeed, these tools allow us to consistently identify a strong interaction between Ezrin's FERM central domain and EGFR's PK domain shown now in the Figure Supplement 2C and Supplement Figure 3C-H. Importantly, these findings generate valuable hypotheses, therefore experimental validation is still necessary. But we prefer to leave it for future studies.

Minor Comments: 

(1) There are several immunoblots that did not have adequate controls:  - In Figure 2D, an input lane should be shown for each of the cell lysates to demonstrate the presence of other proteins in the cell lysate used for the IP.

We have now fixed this inaccuracy in the revised manuscript.

- Figure 3A does not have a loading control. Also, immunoblot quality should be significantly improved.

We have now fixed this inaccuracy in the revised manuscript.

- The HER2 western blot in Figure 5C does not accurately represent the data shown in the quantification graph.

We have now fixed this inaccuracy by replacing HER2 western blot in the revised Figure 5C.

- In Figure 6A, the authors should include an input as a control for the IP. To further support their claim in the model figure, can the authors also probe the IP lysate for Ezrin and Tsc2? If all are indeed in a complex together, they should be present. 

Following this Reviewer’s observation, we add the input as control in the IP in the revised Figure 6A. Moreover, we include the immunoprecipitation data for the EZRIN and TSC2 interaction, accordingly (Figure 6A).

- Phosphorylation sites across figures should be uniformly annotated for consistency and ease of understanding, e.g., pTSC2(S939), pS6K1(T389), and pAKT(S473).

We have now fixed this inaccuracy in the revised text.

(2) There are several microscopy data that lack adequate quantification. For instance, Figures 2E, 2F, 3C, 4A, 5A, and 6F only show very few cells as representative images, which is not sufficient to support their claims. 

We thank the Reviewer for his/her comment that improves our manuscript. Accordingly, we add adequate quantification and statistical analysis in the revised Figures, accordingly.

(3) Some suggestions to improve the readability of the manuscript: 

-  In the abstract (line 32): "Loss of Ezrin was deficient in TSC repression by EGF and culminated in translocation of TSC to lysosomes triggering suppression of mTORC1 signaling." The wording is somewhat confusing, please change such as "Loss of Ezrin was not sufficient to repress TSC by EGF and culminated..." or "Loss of Ezrin blunted EGF-induced TSC suppression and culminated..." 

We apologize for the lack of clarity and now we have fixed this inaccuracy by better elucidating this aspect in the revised manuscript.

-  Figure 3D has a typo in the western blot labeling. Please change Citosol to Cytosol. 

We have now fixed this inaccuracy in the revised text.

-  Line 291: "Moreover, TSC2 resulted activated and AKT/mTOR signaling..." The wording is confusing. 

We have now fixed this inaccuracy in the revised text. The text now reads: “Moreover, we found that TSC2 was dephosphorylated  in response to light in the retina, when inactive Ezrin (Naso et al., 2020) and EGFR are weakly expressed (Figure supplement 6C) as a consequence of a decrease of the AKT/mTORC1 signaling…..)

-  The model in Figure 8 indicates that upon EGF stimulation, the activated Ezrin interacts with EGFR, causing its dissociation from actin filaments and leading to its endosome incorporation. However, the authors did not provide supporting data for this claim. Can the authors either cite literature or provide data for this? Otherwise, the model should be edited to remove actin filaments in the model. 

We have now fixed this inaccuracy by removing actin filaments in the revised model.

Reviewer #2 (Recommendations For The Authors):

The data and written text seem to deal entirely with mTORC1, rather than mTORC2, thus it seems "mTOR" should be changed to "mTORC1" throughout. 

We have now fixed this inaccuracy in the revised manuscript.

For clarification, the TSC protein complex should be referred to as the "TSC complex", whereas "TSC" generally refers to the tumor syndrome Tuberous Sclerosis Complex.

We have now fixed this inaccuracy in the revised manuscript.

Quantification of colocalization would be helpful in all the panels where it is currently missing.

We thank the Reviewer for his/her comment that improves our manuscript. Accordingly, we add adequate quantification of colocalization for each immunofluorescence in the revised Figures, accordingly.

Line 84 typo "thorough" should be "through" 

We have now fixed this inaccuracy in the revised manuscript.

Line 178 - typo 

We have now fixed this inaccuracy in the revised manuscript.

Line 209 - typo 

We have now fixed this inaccuracy in the revised manuscript.

Reviewer #3 (Recommendations For The Authors): 

Fig. 1 The data showing an increase in lysosomal biogenesis suggests an increase in transcriptional activity. This should be confirmed by one or more of the following: 1) Increased TFEB/TFE3 nuclear localization following EZR loss, 2) Increased CLEAR promoter luciferase activity assays, 3) Increased expression of multiple CLEAR transcripts (https://www.science.org/doi/10.1126/science.1174447) or 4) Increased TFEB/ TFE3/ CLEAR gene signatures by RNA seq. Similarly, data showing increased autophagic flux should be confirmed in the presence of chloroquine or bafilomycin. 

We agree with the Reviewer that it is an important concern that helped us to improve the quality of the data presented. It is well established that a major mechanism regulating TFEB activity is represented by the nuclear translocation. We have now carried out new experiments demonstrating that depletion of Ezrin induces TFEB nuclear translocation in Ezrin^-/- cells. These findings are in line with our previous data in which pharmacological inhibition and silencing of Ezrin induced the same cellular phenotype. We also apologize because we have created some confusion, because we already carried out experiments with Bafilomycin to confirm the increase of autophagic flux. Therefore, the blots of autophagic flux were changed for better exposed images in revised Figure supplement 1H and the text was modified to emphasize these findings, accordingly.

Fig 2D, the lanes with EZR -/- cells expressing the EZR mutants should be repeated on the same gel as the first 2 lanes (with the WT and EZR^-/- cells) 

We thank the Reviewer for his/her comment that improves our manuscript. In order to avoid any confusion, when describing the results in Figure 2D, we have now modified the Figure 2D, providing the required controls in the response to Reviewer #1 and #2. We hope the new version of our data will satisfy the Reviewer’s worries.

Fig 2F- The presence of reduced EGFR in intracellular compartments in Ezrin KO/ -/- cells should be quantified, and shown for a 2nd EZR null cell line as well (Ezrin null MEFs) 

We added EGFR quantification in Figure 2F. We have now carried out new experiments demonstrating that EGFR is localized on cytoplasmic membrane in MEF Ezrin KO (Figure supplement 2H), accordingly. 

Fig 2G, did the authors test the effects of EZR depletion on basal and EGF stimulated EGFR autophosphorylation on Y1068 and Y1045 as well as downstream activation of p42/44 ERK MAPK?  Those should be tested in the HeLa system as well as the MEFs cells with EZR KO. 

Following the Reviewer’s request, we have now added western blot data for EGFR autophosphorylation on Y1068 and p42/44 ERK MAPK in Figure 5C. Moreover, we have now added western blot data for p42/44 ERK MAPK on MEF cells in Figure supplement 2F. In contrast, we cannot provide any data for EGFR autophosphorylation on Y1068, because the antibody was not working on proteins from MEF cells.

Also, why would HER3 levels be expected to decrease? There seems to be minimal change in HER3 expression. Also, the significance of increased MK2 phosphorylation should be further elaborated. 

The Reviewer raised justified concerns about the HER3 and MK2. We have discussed these aspects in the "results section”, accordingly. 

Fig 3A- Crosslinking of EGFR is not very apparent in this blot. The crosslinking blots should be repeated 3 times and quantified. 

We certainly agree with the Reviewer on the importance of this issue and now we have fixed this inaccuracy in the revised manuscript. The blots of crosslinking were changed for better exposed images in revised Figure 3, panel A. Moreover, we also properly quantified signals to support our conclusion.

Fig 3D- How were membrane endosomes isolated? This should be stated in the methods. Membrane/ Cytosol and Endosome fractionation showing EGFR levels should be shown in Ezrin null MEFs as well, and membrane expression should be further substantiated with surface biotinylation for cell surface EGFR. 

We now report more information about the method that we used for membrane endosomes isolation in the Materials and Methods section. Following the Reviewer’s request, we also show that EGFR was not localized on endosomes upon EGF on Ezrin null MEFs. This data was reported in the new revised Figure Supplement 2G. Moreover, we have now carried out new experiments demonstrating the membrane localization of EGFR in MEF Ezrin KO cells. These findings are shown in Figure supplement 2H.

Fig 5C: Similar to 2G, EGFR autophosphorylation on Y1068 and Y1045 should also be measured, as well as downstream activation of p42/44 ERK MAPK? 

Following the Reviewer’s request, we have now carried out new experiments to assess the EGFR autophosphorylation on Y1068 and Y1045, as well as downstream activation of p42/44 ERK MAPK.  We added these new data in the revised Figure 5C, accordingly. 

Fig 5D: Similar to 3D, Membrane/ Cytosol and Endosome fractionation showing EGFR levels should be shown in Ezrin null MEFs as well, and further substantiated with surface biotinylation for cell surface EGFR. 

Following the Reviewer’s request, we show that EGFR was not localized on endosomes upon EGF (Figure Supplement 2G). 

Supplement 2E: The blots show lower expression of EGFR and higher MAPK activation in EZR KO cells, contradicting the data in the other cells. 

We apologize because we have created some confusion. It occurred during the preparation of Figure supplement 2E, reflecting image of a previous not finalized version of the Figure. We have now removed the error and replaced with a correct WB panel.

Supplement 2F: The authors should repeat the NSC668394 experiment using: 1) multiple doses, 2) In both the Ezrin KO and null cell lines 3) and repeat 3X to quantify differences in total EGFR. 

We respectfully disagree with the Reviewer and feel that addressing this point by additional studies on dose response of NSC668394, as the Reviewer suggests, is outside the scope of this manuscript. However, we would like to point out that we have already conducted extensive studies on the doseresponse effects of NSC668394 administration in vitro (Patent: WO2020070333A1). 

Moreover, we apologize for not having provided enough information about the number of biological independent replicates for WB analyses. Therefore, to fill this gap of information we have expanded the Material and Methods section, accordingly.

Patent: WO2020070333A1 - Ezrin inhibitors and uses thereof

Fig 6A: The IP experiments should be repeated with Control IgG 

We have now fixed this inaccuracy in the revised manuscript.

Typos: 

(1) Figure 3D: Citosol 

We have now fixed this inaccuracy in the revised manuscript.

(2) Line 216-217: "increased EGFR protein 217 levels on purified membranes and endosomes (Figure 3D and E)" - That should be decreased EGFR on endosomes in accordance with Figure 3D (lower panels) 

We have now fixed this inaccuracy in the revised manuscript.

(3) Abstract: "Consistently, Medaka fish deficient for Ezrin exhibit defective endo-lysosomal pathway" 

We have now fixed this inaccuracy in the revised manuscript.

Author response:

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

Public Review:

Reviewer #1:

(1) To support the finding that texture is not represented in a modular fashion, additional possibilities must be considered. These include (a) the effectiveness and specificity of the texture stimulus and control stimuli, (b) further analysis of possible structure in images that may have been missed, and (c) limitations of imaging resolution.

Thank you for your comments. To address your concerns, we have conducted a new 3T fMRI experiment to demonstrate the effectiveness and specificity of our stimuli, performed further analyses to investigate possible structure of texture-selective activation, and discussed the limitations of imaging resolution.

(a) To demonstrate the effectiveness and specificity of our stimuli, we conducted a new 3T fMRI experiment in five participants using an experimental design and texture families similar to those in Freeman (2013). Six texture stimuli in the 7T experiment were also included. To assess the effectiveness of each stimulus type, different texture families and their corresponding noise patterns were presented in separate blocks for 24 seconds, at a high presentation rate of 5 frames per second. In Figure S7, all texture families showed significantly stronger activation in V2 compared to their corresponding noise patterns, even for those that ‘appeared’ to have residual texture (e.g., the third texture family). These results demonstrate that our texture vs. noise stimuli were effective in producing texture-selective activations in area V2. Compared to the 7T results, the 3T data showed a notable increase in texture-selective activations in V2, likely due to increased stimulus presentation speed (1.25 vs. 5 frames/second). Future studies should use stimuli with faster presentation speed to validate our results in the 7T experiment.

(b)Thank you for pointing out the possible structures of texture-selective activations in the peripheral visual field (Figure S1). In further analyses, we also found stronger texture selectivity in more peripheral visual fields (Figure 2D), and there were weak but significant correlations in the texture-noise activation patterns during split-half analysis (Author response image 2). Although this is not strong evidence for columnar organization of naturalistic textures, it suggests a possibility for modular organizations in the peripheral visual field.

(c) Although our fMRI result at 1-mm isotropic resolution did not show strong evidence for modular processing of naturalistic texture in V2 stripe columns, this does not exclude the possibility that smaller modules exist beyond the current fMRI resolution. We have discussed this possibility in the revised manuscript.

We hope this response clarifies our findings, and we have revised the conclusions in the manuscript accordingly.

(2) More in-depth analysis of subject data is needed. The apparent structure in the texture images in peripheral fields of some subjects calls for more detailed analysis. e.g Relationship to eccentricity and the need for a 'modularity index' to quantify the degree of modularity. A possible relationship to eccentricity should also be considered.

Based on your recommendations, we have performed further analysis and found interesting results regarding the modularity index in relation to eccentricity. As shown in Figure 2D, the texture-selectivity index increased as eccentricity. This may suggest a higher possibility of modular organization for texture representation in the peripheral compared to central visual fields. We have updated our results in Figure 2C, and discussed this possibility in the revised manuscript.

(3) Given what is known as a modular organization in V4 and V3 (e.g. for color, orientation, curvature), did images reveal these organizations? If so, connectivity analysis would be improved based on such ROIs. This would further strengthen the hierarchical scheme.

Following your recommendations, we have conducted further analysis to investigate the potential modular organizations in V4 and V3ab. In Figure S9 (Figure S9), vertices that are most responsive to color, disparity and texture were shown in a representative subject. Indeed, texture-selective patches can be found in both V4 and V3ab, along with the color- and disparity-selective patches. We agree with you that there should be pathway-specific connectivity among the same type of functional modules. In the informational connectivity analyses, we already used highly informative voxels by feature selection, which should mainly represent information from the modular organizations in these higher visual areas.

Reviewer #2:

(1) In lines 162-163, it is stated that no clear columnar organization exists for naturalistic texture processing in V2. In my opinion, this should be rephrased. As far as I understand, Figure 2B refers to the analysis used to support the conclusion. The left and middle bar plots only show a circular analysis since ROIs were based on the color and disparity contrast used to define thin and thick stripes. The interesting graph is the right plot, which shows no statistically significant overlap of texture processing with thin, thick, and pale stripe ROIs. It should be pointed out that this analysis does not dismiss a columnar organization per se but instead only supports the conclusion of no coincidence with the CO-stripe architecture.

Thank you for your suggestions. Reviewer #1 also raised a similar concern. We agree that there may be a smaller functional module of textures in area V2 at a finer spatial scale than our fMRI resolution. We have rephrased our conclusions to be more precise.

(2) In Figure 3, cortical depth-dependent analyses are presented for color, disparity, and texture processing. I acknowledge that the authors took care of venous effects by excluding outlier voxels. However, the GE-BOLD signal at high magnetic fields is still biased to extravascular contributions from around larger veins. Therefore, the highest color selectivity in superficial layers might also result from the bias to draining veins and might not be of neuronal origin. Furthermore, it is interesting that cortical profiles with the highest selectivity in superficial layers show overall higher selectivity across cortical depth. Could the missing increase toward the pial surface in other profiles result from the ROI definition or overall smaller signal changes (effect size) of selected voxels? At least, a more careful interpretation and discussion would be helpful for the reader.

We agree with you that there will be residual venous effects even after removing voxels containing large veins. However, calculating the selectivity index largely removed the superficial bias (Figure 3). In the revised manuscript, we discussed the limitations of cortical depth-dependent analysis using GE-BOLD fMRI.

In Line 397-403: “Due to the limitations of the T2*w GE-BOLD signal in its sensitivity to large draining veins (Fracasso et al., 2021; Parkes et al., 2005; Uludag & Havlicek, 2021), the original BOLD responses were strongly biased towards the superficial depth in our data (Figure S8). Compared to GE-BOLD, VASO-CBV and SE-BOLD fMRI techniques have higher spatial specificity but much lower sensitivity (Huber et al., 2019). As shown in a recent study (Qian et al., 2024), using differential BOLD responses in a continuous­­ stimulus design can significantly enhance the laminar specificity of the feature selectivity measures in our results (Figure 3).”

It is unlikely that the strongest color selectivity index in the superficial depth is a result of stronger signal change or larger effect size in this condition. As shown by the original BOLD responses in Figure S8, all stimulus conditions produced robust activations that strongly biased to the superficial depth. High texture selectivity was also found in V4 and V3ab across cortical depth, which showed a flat laminar profile.

(3) I was slightly surprised that no retinotopy data was acquired. The ROI definition in the manuscript was based on a retinotopy atlas plus manual stripe segmentation of single columns. Both steps have disadvantages because they neglect individual differences and are based on subjective assessment. A few points might be worth discussing: (1) In lines 467-468, the authors state that V2 was defined based on the extent of stripes. This classical definition of area V2 was questioned by a recent publication (Nasr et al., 2016, J Neurosci, 36, 1841-1857), which showed that stripes might extend into V3. Could this have been a problem in the present analysis, e.g., in the connectivity analysis? (2) The manual segmentation depends on the chosen threshold value, which is inevitably arbitrary. Which value was used?

A previous study showed that the retinotopic atlas of early visual areas (V1-V3) aligned very well across participants on the standard surface after surface-based registration by the anatomical landmarks (Benson 2018). Thus, the group-averaged atlas should be accurate in defining the boundaries of early visual areas. To directly demonstrate the accuracy of this method, retinotopic data were acquired in five participants in a 3T fMRI experiment. A phase-encoded method was used to define the boundaries of early visual areas (black lines in Author response image 1), which were highly consistent with the Benson atlas.

Although a few feature-selective stripes may extend into V3, these stripe patterns were mainly represented in V2. Thus, the signal contribution from V3 is likely to be small and should not affect the pattern of results. The activation map threshold for manual segmentation was abs(T)>2. We have clarified this in the revised methods.

Author response image 1.

Retinotopic ROIs defined by the Benson atlas (left) and the polar angle map (right) of the representative subject. Black lines denote the boundaries of early visual areas based on the retinotopic map from the subject.

Benson, N. C., Jamison, K. W., Arcaro, M. J., Vu, A. T., Glasser, M. F., Coalson, T. S., Van Essen, D. C., Yacoub, E., Ugurbil, K., Winawer, J., & Kay, K. (2018). The Human Connectome Project 7 Tesla retinotopy dataset: Description and population receptive field analysis. J Vis, 18(13), 23. https://doi.org/10.1167/18.13.23

(4) The use of 1-mm isotropic voxels is relatively coarse for cortical depth-dependent analyses, especially in the early visual cortex, which is highly convoluted and has a small cortical thickness. For example, most layer-fMRI studies use a voxel size of around isotropic 0.8 mm, which has half the voxel volume of 1 mm isotropic voxels. With increasing voxel volume, partial volume effects become more pronounced. For example, partial volume with CSF might confound the analysis by introducing pulsatility effects.

We agree that a 1-mm isotropic voxel is much larger in volume than a 0.8-mm isotropic voxel, but the resolution along the cortical depth is not a big difference. In addition to our study, a previous study showed that fMRI at 1-mm isotropic resolution is capable of resolving cortical depth-dependent signals (Roefs et al., 2024; Shao et al., 2021). We have discussed these issues about fMRI resolution in the revised manuscript.

In Line 403-408: “Compared to the submillimeter voxels, as used in most laminar fMRI studies, our fMRI resolution at 1-mm isotropic voxel may have a stronger partial volume effect in the cortical depth-dependent analysis. However, consistent with our results, previous studies have also shown that 7T fMRI at 1-mm isotropic resolution can resolve cortical depth-dependent signals in human visual cortex (Roefs et al., 2024; Shao et al., 2021).”

Shao, X., Guo, F., Shou, Q., Wang, K., Jann, K., Yan, L., Toga, A. W., Zhang, P., & Wang, D. J. J. (2021). Laminar perfusion imaging with zoomed arterial spin labeling at 7 Tesla. NeuroImage, 245, 118724. https://doi.org/10.1016/j.neuroimage.2021.118724

Roefs, E. C., Schellekens, W., Báez-Yáñez, M. G., Bhogal, A. A., Groen, I. I., van Osch, M. J., ... & Petridou, N. (2024). The Contribution of the Vascular Architecture and Cerebrovascular Reactivity to the BOLD signal Formation across Cortical Depth. Imaging Neuroscience, 2, 1–19.

(5) The SVM analysis included a feature selection step stated in lines 531-533. Although this step is reasonable for the training of a machine learning classifier, it would be interesting to know if the authors think this step could have reintroduced some bias to draining vein contributions.

We excluded vertices with extremely large signal change and their corresponding voxels in the gray matter when defining ROIs. The same number of voxels were selected from each cortical depth for the SVM analysis, thus there was no bias in the number of voxels from the superficial layers susceptible to large draining veins.

Reviewer #3:

The authors tend to overclaim their results.

Re: Thank you for your comments. We added more control analyses to strengthen our findings, and gave more appropriate discussion of results.

Recommendations for the authors:

Reviewer #1:

(1) Controls: There is a bit more complexity than is expressed in the introduction. The authors hypothesize that the emergence of computational features such as texture may be reflected in specialized columns. That is, if texture is generated in V2, there may be texture columns (perhaps in the pale stripes of V2); but if generated at a higher level, then no texture columns would be needed. This is a very interesting and fundamental hypothesis. While there may be merit to this hypothesis, the demonstration that color and disparity are modular but not texture falls short of making a compelling argument. At a minimum, the finding that texture is not organized in V2 requires additional controls. (a) To boost the texture signal, additional texture stimuli or a sequence of multiple texture stimuli per trial could be considered. (b) Unfortunately, the comparison noise pattern also seems to contain texture; perhaps a less textured control could be designed. (c) It also appears that some of the texture images in Supplementary Figure S1 contain possible structure, e.g. in more peripheral visual fields. (d) Is it possible that the current imaging resolution is not sufficient for revealing texture domains? (e) Note that 'texture' may be a property that defines surfaces and not contours. Thus, while texture may have orientation content, its function may be associated with the surface processing pathways. A control stimulus might contain oriented elements of a texture stimulus that do not elicit texture percept; such a control might activate pale and/or thick stripes (both of which contain orientation domains), while the texture percept stimulus may activate surface-related bands in V4.

Thank you for your suggestions. They are extremely helpful in improving our manuscript. For the controls you mentioned in (a-d), we discussed them in the public review that we also attached below.

(a) and (b): To demonstrate the effectiveness and specificity of our stimuli, we conducted a new 3T fMRI experiment in five participants using an experimental design and texture families similar to those in Freeman (2013). All texture stimuli in the 7T experiment were also included. To assess the effectiveness of each stimulus type, different texture families and their corresponding noise patterns were presented in separate blocks for 24 seconds, at a high presentation rate of 5 frames per second. In Figure S7, all texture families showed significantly stronger activation in V2 compared to their corresponding noise patterns, even for those that ‘appeared’ to have residual texture (e.g., the third texture family). These results suggest that our texture stimuli were effective in producing texture-selective activations in area V2 compared to the noise control. Compared to the 7T results, the 3T data showed a notable increase in texture-selective activations in V2, likely due to the increased stimulus presentation speed (1.25 vs. 5 frames/second). Weak texture activations might preclude the detection of columnar representations in the 7T experiment.

(c) Thank you for pointing out the possible structures of texture-selective activations in the peripheral visual field (Figure S1). In further analyses, we also found stronger texture selectivity in more peripheral visual fields (Figure 2D), and there were weak but significant correlations in the texture-noise activation patterns during split-half analysis (Author response image 2). Although these are not strong evidence for columnar organization of naturalistic textures, it suggests a possibility for such organizations in the peripheral visual field.

(d) Although our fMRI result at 1-mm isotropic resolution did not show strong evidence for modular processing of naturalistic texture in V2 stripe columns, this does not exclude the possibility that smaller modules exist beyond the current fMRI resolution. We have discussed these limitations in the revised manuscript.

We fully agree with your explanation in (e). It fits our data very well. Both texture and control stimuli strongly activated the CO-stripes (Figure 2 and Figure 2D), while modular organizations for texture were found in V4 and V3ab (Figure S9). We have discussed this explanation in the revised manuscript.

In Line 371-374: “Consistently, our pilot results also revealed modular organizations for textures in V4 and V3ab (Figure S9). These texture-selective organizations may be related to surface representations in these higher order visual areas (Wang et al., 2024).”

(2) Overly simple description of FF, FB circuitry. The classic anatomical definition of feedforward is output from a 'lower' area, in most cases predominantly arising from superficial layers and projecting to middle layers of a 'higher area' (Felleman and Van Essen 1991). This description holds for V1-to-V2, V2-to-V3, and V2-to-V4. [Note there are also feedforward projections from central 5 degrees of V1-to-V4 (cf. Ungerleider) as well as V3-to-V4.] The definition of feedback can be more varied but is generally considered from cells in superficial and deep layers of 'higher' areas projecting to superficial and deep layers of 'lower' areas. Feedback inputs to V1 heavily innervate Layer 1 and superficial Layer 2, as well as the deep layers. Note that feedback connections from V2 to V1, similar to that from V1 to V2, are functionally specific, i.e. thin-to-blob and pale/thick-to interblob (Federer...Angelucci 2021, Hu...Roe 2022). Thus, current views are moving away from the dogma that feedback is diffuse. Recognition that feedback may be modular introduces new ideas about analysis.

Thanks for your detailed recommendations. We have expanded the discussion of circuit models of functional connectivity in the introduction. Our model and experiments primarily aim to investigate how higher-level areas provide feedback to the V2 area. While we acknowledge that feedback may indeed be functionally specific, our methodology has some certain advantages: it ensures signal stability and avoids the double-dipping issue. Meanwhile, it also focuses on voxels with high feature selectivity, which may already be included in the modular organizations of early visual areas. In the functional connectivity analysis, we performed feature selection to use the most informative voxels. These voxels with high feature selectivity should already be included in the modular organizations of early visual areas. Identifying functionally specific feedback connections between modular areas will be an important and meaningful work for future research. We have added a discussion of this topic in the revised manuscript.

In Line 136-138: “Only major connections were shown here. There are also other connections, such as V1 interblobs projecting to thick stripes (Federer et al., 2021; Hu & Roe, 2022; Sincich and Horton, 2005).”

(3) Imaging superficial layers: Although removal of the top layer of cortical voxels (top 5% of voxels) is a common method for dealing with surface vascular artifact contribution to BOLD signal, it likely removes a portion of the Layer 1&2 feedback signals. Is this why the authors define feedback and deep layer to deep layer? If so, both superficial and deep-layer data in Figure 4 should be explicitly explained and discussed.

Thank you for pointing this out. We would like to clarify the surface-based method removing vascular artifact. The vertices influenced by large pial veins were first defined on the cortical surface, and then voxels were removed from the entire columns corresponding to these vertices to avoid sampling bias along the cortical depth. Thus, there should be complete data from all cortical depths for the remaining columns. We defined the feedback connectivity from deep layers to deep layers because it represents strong feedback connections according to literature (Markov et al., 2013; Ullman, 1995) and also avoids confounding the feedforward signals from superficial layers.

Markov, N. T., Vezoli, J., Chameau, P., Falchier, A., Quilodran, R., Huissoud, C., Lamy, C., Misery, P., Giroud, P., Ullman, S., Barone, P., Dehay, C., Knoblauch, K., & Kennedy, H. (2014). Anatomy of hierarchy: feedforward and feedback pathways in macaque visual cortex. The Journal of comparative neurology, 522(1), 225–259. https://doi.org/10.1002/cne.23458

Ullman S. (1995). Sequence seeking and counter streams: a computational model for bidirectional information flow in the visual cortex. Cerebral cortex, 5(1), 1–11. https://doi.org/10.1093/cercor/5.1.1

(4) More detail on other subjects in Figure S1. Ten subjects conducted visual fixation and used a bite bar. Imaging data are illustrated in detail from one subject and the remaining subjects are depicted in graphs and in Supplemental Figure S1. Please provide arrowheads in each image to help guide the reader. Some kind of summary or index of modularity would also be helpful.

Thanks for your suggestions. There are arrowheads in each image in our original manuscript and we have revised Figure S1 for better illustration. Additionally, we have added a table summarizing the number of stripes to provide a clearer overview.

(5) How are ROIs in V3ab and V4 defined? V2 ROIs were defined (thin, thick, and pale stripe), but V3ab and V4 averaged across the whole area. Why not use the most activated "domains" from V3ab and V4? How does this influence connectivity analysis?

Thank you for your question. We defined V4 and V3ab on the cortical surface using a retinotopic atlas (Benson 2018), which has been shown to be quite accurate in defining ROIs for the early visual areas. Since all ‘domains’ showed robust BOLD activation to our stimuli, we used voxels from the entire ROI in the depth-dependent analysis. In the functional connectivity analysis, we used the most informative voxels by feature selection, which should already be included in the feature domains.

Minor:

English language editing is needed.

Thank you for your feedback. We have carefully revised the manuscript for clarity and readability.

Line 31 "its" should be "their".

Thank you. We have corrected "its" to "their".

Replace 'representative subject' with 'subject'.

We have replaced "representative subject" with "subject" in the manuscript.

Replace 'naturalistic texture' with 'texture'.

Thank you for your suggestion. The textures used in our experiment were generated based on the algorithm by Portilla and Simoncelli (2000), and the term "naturalistic texture" was used to be consistent with literature. The textures used in our study are different from traditional artificial textures, as they contain higher-order statistical dependencies. Following your recommendations, we have replaced ‘naturalistic texture’ with ‘texture’ in some places in the main text to improve readability.

Typo: Line 126, Fig 2B should be 1B.

Thank you. We have corrected "Fig 2B" to "Fig 1B" in Line 128.

Fig. 2A: point out where are texture domains in anterior V2.

The texture-selective activations in anterior V2 (corresponds to peripheral visual field) have been highlighted by arrowheads.

Fig 2B, 3 legend: Round symbols are for each subject?

Yes, the round symbols in Figures 2B represent data for individual participants. We have revised the legend for clarity.

Fig. 3: Disparity and texture values do not look different across depth (except may the V2 texture values).

While the difference in feature selectivity is small across cortical depths, they are highly consistent across participants. We have provided a figure showing the original BOLD responses in the revised manuscript (Figure S8 and Figure S8). Data from individual subjects were also available at Open Science Framework (OSF, https://doi.org/10.17605/OSF.IO/KSXT8 (‘rawBetaValues.mat’ in the data directory)).

Line 57-59 The statement is not strictly accurate. V1 also has color, orientation, and motion representations.

Thank you for your feedback. Our statement was intended to convey that M and P information from the geniculate input are transformed into representations of color, orientation, disparity, and motion in the primary visual cortex. We have clarified this point in the revised manuscript.

In Line 58-60: “In the primary visual cortex (V1), the M and P information from the geniculate input are transformed into higher-level visual representations, such as motion, disparity, color, orientation, etc. (Tootell & Nasr, 2017).”

Fig. 1B V1 interblobs also project to thick stripes (Sincich and Horton).

Thank you for the additional information. We appreciate your input. Our figure is intended as a simplified schematic and does not fully represent all the connections. We have discussed this reference in the revised manuscript.

In Line 136-138: “Only major connections were shown here. There are also other connections, such as V1 interblobs projecting to thick stripes (Federer et al., 2021; Hu & Roe, 2022; Sincich and Horton, 2005).”

Line 207 "suggesting that both local and feedforward connections are involved in processing color information in area V2." Logic? English?

Thank you for pointing this out. The superficial layers are involved in local intracortical processing by lateral connections and also send output to higher order visual areas along the feedforward pathway. Thus, the strongest color selectivity in the superficial depth of V2 supports that color information was processed in local neural circuits in area V2 and transmitted to higher order areas along the feedforward pathway. We have revised the manuscript for clarity.

In Line 241-245: “According to the hierarchical model, the strongest color selectivity in the superficial cortical depth is consistent with the fact that color blobs locate in the superficial layers of V1 (Figure 1B, Felleman & Van Essen, 1991; Hubel & Livingstone, 1987; Nassi & Callaway, 2009). The strongest color selectivity in superficial V2 suggests that both local and feedforward connections are involved in processing color information (Figure 1C).”

Line 254 "Laminar". Please use "cortical depth" or explicitly state that 'laminar' refers to superficial, middle, and deep as defined by cortical depth.

Thank you for your suggestion. We have clarified the term "laminar" in the manuscript as referring to superficial, middle, and deep layers as defined by cortical depth.

In Line 96-99: “To better understand the mesoscale functional organizations and neural circuits of information processing in area V2, the present study investigated laminar (or cortical depth-dependent) and columnar response profiles for color, disparity, and naturalistic texture in human V2 using 7T fMRI at 1-mm isotropic resolution.”

Fig. S5 Please add a unit of isoluminance.

Thank you for your suggestion. Supplementary Figure S10A and S10B illustrate the blue-matched luminance levels in RGB index. In our isoluminance experiment, blue was set as the reference color (RGB [0 0 255]) to measure the red and gray isoluminance.

Line 448-449 To make this rationale clearer, refer to:

Wang J, Nasr S, Roe AW, Polimeni JR. 2022. Critical factors in achieving fine‐scale functional MRI: Removing sources of inadvertent spatial smoothing. Human Brain Mapping. 43:3311-3331.

Thank you for your suggestion. We have added this reference to better support the rationale of data analysis.

Reviewer #2:

(1) Line 126 should refer to Figure 1B.

Thank you. We have corrected the reference in the revised manuscript as Figure 1B.

(2) Even if only one naturalistic texture session was acquired per participant, it might be interesting to see the within-session repeatability by, e.g., splitting the texture runs into two halves.

Thank you for your suggestion. We performed a split-half correlation analysis for participants who completed 10 runs in the naturalistic texture session. The result from one representative subject was shown in the figure below (for other participants, r = 0.38, 0.38, 0.24, and 0.23, respectively).

Author response image 2.

Split-half correlations for the texture-selective activation maps in a representative subject (S01) in V2.

(3) Unfortunately, Figure S2 only shows the stripe ROIs but not V3ab or V4 ROIs. Including another figure that shows all ROIs in more detail would be interesting.

Thank you for your suggestion. We have included a figure showing the ROIs for V4 and V3ab (the black dotted lines in Figure S9).

(4) It would be helpful for the reader to have a more detailed discussion about methodological limitations, including the unspecificity of the GE-BOLD signal (Engel et al., 1997, Cereb Cortex, 7, 181-192; Parkes et al., 2005, MRM, 54, 1465-1472; Fracasso et al., 2021, Prog Neurobiol, 202, 102187) and the used voxel sizes.

Thank you for your suggestion. We have added a more detailed discussion about the methodological limitations, including the unspecificity of the GE-BOLD signal and the voxel sizes used.

In Line 397-408: “Due to the limitations of the T2*w GE-BOLD signal in its sensitivity to large draining veins (Fracasso et al., 2021; Parkes et al., 2005; Uludag & Havlicek, 2021), the original BOLD responses were strongly biased towards the superficial depth in our data (Figure S8). Compared to GE-BOLD, VASO-CBV and SE-BOLD fMRI techniques have higher spatial specificity but much lower sensitivity (Huber et al., 2019). As shown in a recent study (Qian et al., 2024), using differential BOLD responses in a continuous¬¬ stimulus design can significantly enhance the laminar specificity of the feature selectivity measures in our results (Figure 3). Compared to the submillimeter voxels, as used in most laminar fMRI studies, our fMRI resolution at 1-mm isotropic voxel may have a stronger partial volume effect in the cortical depth-dependent analysis. However, consistent with our results, previous studies have also shown that 7T fMRI at 1-mm isotropic resolution can resolve cortical depth-dependent signals in human visual cortex (Roefs et al., 2024; Shao et al., 2021).”

(5) If I understand correctly, different numbers of runs/sessions were acquired for different subjects. It would be good to discuss if this could have impacted the results, e.g., different effect sizes could have biased the manual ROI definition.

Thank you for your suggestion. Although there were differences in the number of runs/sessions acquired for different subjects, there were at least four runs of data for each experiment, which should be enough to examine the within-subject effect. We have discussed this point in the revised manuscript.

In Line 481-484: “Although the number of runs were not equal across participants, there were at least four runs (twenty blocks for each stimulus condition) of data in each experiment, which should be sufficient to investigate within-subject effects.”

(6) It would be good to add the software used for layer definition. Was it Laynii?

We have provided more details in the revised methods.

In Line 523-526: “An equi-volume method was used to calculate the relative cortical depth of each voxel to the white matter and pial surface (0: white matter surface, 1: pial surface, Supplementary Figure S11A), using mripy (https://github.com/herrlich10/mripy).”

(7) It would be interesting to see (at least for one subject) the contrasts of color-selective thin stripes and disparity-selective thick stripes from single sessions to demonstrate the repeatability of measurements.

Thank you for your suggestion. We have shown the test-retest reliability of the response pattern of color-selective thin stripes and disparity-selective thick stripes in a representative subject in Figure S5.

(8) By any chance, do the authors also have resting-state data from the same subjects? It would be interesting to see the connectivity analysis between stripes and V3ab, V4 with resting-state data.

Thank you for your suggestion. Unfortunately, we do not have resting-state data from the same subjects at this time. We agree with you that layer-specific connectivity analysis with resting-state data is very interesting and worth investigating in future studies.

Reviewer #3:

(1) For investigating information flow across areas, the authors rely on layer-specific informational connectivity analyses, which is an exciting approach. Covariation in decoding accuracy for a specific dependent variable between the superficial layers of a lower area and the middle layer of a higher area is taken as evidence for feedforward connectivity, whereas FB was defined as the connection between the two deep layers. Yet this method is not assumption-free. For example, the canonical idea (Figure 1C) of FF terminals exclusively arriving in layer 4 and FB terminals exclusively terminating in supra-or infragranular layers is not entirely correct. This is not even the case for area V1 - see for example Kathy Rockland's exquisite tractography studies, showing that even single axons with branches terminating in different layers. Also, feedback signals not only arrive in the deep layers of a lower area. Although these informational connectivity analyses can be suggestive of information flow, this reviewer doubts it can be considered as conclusive evidence. Therefore, the authors should drastically tone down their language in this respect, throughout the text. They present suggestive, not conclusive evidence. To obtain truly conclusive evidence, one likely has to perform laminar electrophysiological recordings simultaneously across multiple areas and infer the directionality of information flow using, for example, granger causality.

Thank you for pointing out this important issue. In our response to a previous question (Reviewer #1, the 2nd comment), we have discussed other possible connections in addition to the canonical feedforward and feedback pathways. In the revised manuscript, the conclusion has been toned down to properly reflect our findings. However, we would also like to emphasize that our conclusion about laminar circuits was supported by converging lines of evidence. For example, in addition to the depth-dependent connectivity results, the role of feedback circuit in processing texture information was also supported by greater selectivity in V4 than V2, and the strongest deep layer selectivity in V2 (Figure 3C).

(2) In the same realm, how reproducible are the information connectivity results? In the first part of the study, the authors performed a split-half analyses. This should be also done for Figure 4.

Thank you for your suggestion. We have performed a split-half analysis for the informational connectivity results. As shown in Author response image 3, the results for the color experiment were robust and reproducible, while the disparity and texture connectivity results were less consistent between the two halves. The results from the second half (Author response image 3, below) are more consistent with the original findings (Figure 4). Overall, the pattern of results were qualitatively similar between the two halves. The inconsistency may be due to the fact that some participants had only four runs of data, which could make the split-half analysis less reliable.

Author response image 3.

Split-half analysis of informational connectivity.

(3) Most of the other layer-specific claims (not the ones about the flow of information) are based on indices. It is unclear which ROIs contributed to these indices. Was it the entire extent of V1, V2, ...? Or only the visually-driven voxels within these areas? How exactly were the voxels selected? For V2, it would make sense to calculate the selectivity indices independently for the disparity and color-selective (putative) thick and (putative) thin stripe compartments, respectively. Adding voxels of non-selective compartments (e.g. putative thick stripe voxels for calculating the color-index; or adding putative thin-strip voxels for calculating the disparity index), will only add noise.

In the revised manuscript, we have clarified that we selected the entire ROI in the depth-dependent analysis. Since our study does not have an independent functional localizer, using the entire ROI avoids the problem of double dipping. The processing of visual features is not confined solely to specific stripes. We have also provided a more comprehensive explanation of this issue in the discussion section.

In Line 541-544: “For the cortical depth-dependent analyses in Figure 3, we used all voxels in the retinotopic ROI. Pooling all voxels in the ROI avoids the problem of double-dipping and also increases the signal-to-noise ratio of ROI-averaged BOLD responses.”

(4) It is apparent from Figure 3, that the indices are largely (though not exclusively) driven by 2 subjects. Therefore, this reviewer wishes to see the raw data in addition to a table for calculating the color, disparity, and texture selectivity indices -along with the number of voxels that contributed to it.

Thank you for your suggestion. We have provided a figure showing the original BOLD responses (Figure S8 and Figure S8). Data from individual subjects were also available at Open Science Framework (OSF, https://doi.org/10.17605/OSF.IO/KSXT8 (‘rawBetaValues.mat’ in the data directory)).

Minor:

(1) I typically find inferences about 'layer fMRI' vastly overstated. We all know that fMRI does not (yet) provide laminar-specific resolution, i.e., whereby meaningful differences in fMRI signals can be extracted from all 6 individual layers of neocortex, without partial volume effects, or without taking into account pre-and postsynaptic contributions of neurons to the fMRI signal (the cell bodies may very well lay in different layers than the dendritic trees etc.), or without taking into account the vascular anatomy, etc. The authors should use the term cortical depth-dependent fMRI throughout the text -as they do in the abstract and intro.

Thank you for pointing out this important issue. We have now defined the meaning of layer or laminar as “cortical depth-dependent” in the introduction, to be consistent with the terminology in most published papers on this topic.

(2) 1st sentence abstract: I disagree with this statement. The parallel streams in intermediate-level areas are probably equally well studied as the geniculostriate pathway -already starting with the seminal work of Hubel, Livingstone, and more recently by Angelucci and co-workers who looked in detail at the anatomical and functional interactions across sub-compartments of V1 and V2.

Thank you for your feedback. In the revised manuscript, we have removed the term "much" from the first sentence of the abstract. Although there have been seminal studies of V2 sub-compartments in monkeys, only a few fMRI studies investigated this issue in humans.

(3) The authors show inter-session correlations for color and disparity. This reviewer would like to see test-retest images since the explained variance is not terribly good. Also, show the correlation values for the inter-session texture beta values.

Thank you for your suggestion. We have performed the test-retest reliability analysis of texture-selective patterns in the response to a previous question (Reviewer #2, the 2nd comment, Author response image 2).

(4) The stripe definitions are threshold dependent. Please clarify whether the reported results are threshold-independent.

Thank you for your question. To address your concern, we defined the stripe ROIs using different thresholds, and the results remained consistent. Specifically, we ranked the voxels in manually defined stripe ROIs by the color-disparity response. We then defined the lowest 10% as the thick stripe voxels, the highest 10% as thin stripe voxels, and the middle 10% as pale stripe voxels. Additionally, we adjusted the thresholds to 20% and 30% to define the three stripes (with 30% being the least strict threshold). Feature selectivities at different thresholds were shown in Figure S6 (from left to right: 10%, 20%, 30%). Notably, in all threshold conditions, there was no significant difference in texture selectivity across different stripes.

(5) How were the visual areas defined?

In the revised manuscript, we have provided a detailed description about methods.

In Line 531-535: “ROIs were defined on the inflated cortical surface. Surface ROIs for V1, V2, V3ab, and V4 were defined based on the polar angle atlas from the 7T retinotopic dataset of Human Connectome Project (Benson et al., 2014, 2018). Moreover, the boundary of V2 was edited manually based on columnar patterns. All ROIs were constrained to regions where mean activation across all stimulus conditions exceeded 0.”

(6) "According to the hierarchical model in Figure 1B and 1C, the strongest color selectivity in the superficial cortical depth is consistent with the fact that color blobs mainly locate in the superficial layers of V1, suggesting that both local and feedforward connections are involved in processing color information in area V2." But color-selective activation within V2 could be also consistent with feedback from other areas (some of which were not covered in the present experiments) -the more since most parts of the brain were not covered (i.e. a slab of 4 cm was covered)?

Thank you for reminding us about this issue. We have discussed the possibility of feedback influence in explanation of the superficial bias of color selectivity in area V2.

Author response:

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

Point-by-point responses to the reviewers' comments:

All three reviewers found our analysis of focal adhesion-associated oncogenic pathways (Figs 3 and S3) to be inconsistent (Reviewer 1), not convincing/consistent (Reviewer 2, #2), and too variable and not well supported (Reviewer 3, #2). This was probably the basis for the eLife assessment, which stated: “However, the study is incomplete because the downstream molecular activities of PLECTIN that mediate the cancer phenotypes were not fully evaluated.” We agree with the reviewers that the degree of attenuation of the FAK, MAP/Erk, and PI3K/AKT signaling pathways differs depending on the cell line used (Huh7 and SNU-475) and the mode of inactivation (CRISPR/Cas9-generated plectin KO, functional KO (∆IFBD), and organoruthenium-based inhibitor plecstatin-1). However, we do not share the reviewers' skepticism about the unconvincing nature of the data presented.

Several previous studies have shown that plectin inactivation invariably leads to dysregulation of cell adhesions and associated signaling pathways in various cell systems. The molecular mechanisms driving these changes are not fully understood, but the most convincingly supported scenarios are uncoupling of keratin filaments (hemidesmosomes; (Koster et al., 2004)) and vimentin filaments (focal adhesions; (Burgstaller et al., 2010; Gregor et al., 2014)) from adhesion sites in conjunction with altered actomyosin contractility (Osmanagic-Myers et al., 2015; Prechova et al., 2022; Wang et al., 2020). This results in altered morphometry (Wang et al., 2020), dynamics (Gregor et al., 2014), and adhesion strength (Bonakdar et al., 2015) of adhesions. These changes are accompanied by reduced mechanotransduction capacity and attenuation of downstream signaling such as FAK, Src, Erk1/2, and p38 in dermal fibroblasts (Gregor et al., 2014); decrease in pFAK, pSrc, and pPI3K levels in prostate cancer cells (Wenta et al., 2022); increase in pErk and pSrc in keratinocytes (Osmanagic-Myers et al., 2006); decrease in pERK1/2 in HCC cells (Xu et al., 2022) and head and neck squamous carcinoma cells (Katada et al., 2012).  

Consistent with these published findings, we show that upon plectin inactivation, the HCC cell line SNU475 exhibits aberrant cytoskeletal organization (vimentin and actin; Figs 4A-D, S4A-F), altered number, topography and morphometry of focal adhesions (Figs 4A, E-G, S4H,I), and ineffective transmission of traction forces (Fig 4H,I). Similar, although not quantified, phenotypes are present in Huh7 with inactivated plectin (data not shown). It is worth noting, that even robust cytoskeletal (e.g. #ventral stress fibers, Fig 4A,D and vimentin architecture, Fig S4A-C) and focal adhesion (%central FA, Fig 4A,E) phenotypes differ significantly between different modes of plectin inactivation and would certainly do so if compared between cell lines. These phenotypes are heterogeneous but not inconsistent. Interestingly, both SNU-475 and Huh7 plectin-inactivated cells show similar functional consequences such as prominent decrease in migration speed (Fig 5B). This suggests that while specific aspects of cytoarchitecture are differentially affected in different cell lines, the functional consequences of plectin inactivation are shared between HCC cell lines.

It is therefore not surprising that the activation status of downstream effectors, resulting from different degrees of cytoskeletal and focal adhesion reconfiguration, is not identical (or even comparable) between cell lines and treatment conditions. Furthermore, we compare highly epithelial (keratin- and almost no vimentin-expressing) Huh7 cells with highly dedifferentiated (low keratin- and high vimentinexpressing) SNU-475 cells, which differ significantly in their cytoskeleton, adhesions, and signaling networks. Alternative approaches to plectin inactivation are not expected to result in the same degree of dysregulation of specific signaling pathways. Effects of adaptation (CRISPR/Cas9-generated KOs and ∆IFBDs), engagement of different binding domains (CRISPR/Cas9-generated ∆IFBDs), and pleiotropic modes of action (plecstatin-1) are expected.

In our study, we provide the reader with an unprecedented complex comparison of adhesion-associated signaling between WT and plectin-inactivated HCC cell lines. First, we compared the proteomes of WT, KO and PST-treated WT SNU-475 cells using MS-based shotgun proteomics and phosphoproteomics (Fig 3A-C). Second, we extensively and quantitatively immunoblotted the major molecular denominators of MS-identified dysregulated pathways (such as “FAK signaling”, “ILK signaling”, and “Integrin signaling”) with the following results. Data (shown in Figs 3D and S3C) are expressed as a percentage of untreated WT, with downregulated values are highlighted in red:

Author response table 1.

In addition, we show dysregulated expression (mostly downregulation) of focal adhesion constituents ITGβ1 and αv, talin, vinculin, and paxilin which nicely complements fewer and larger focal adhesions in plectin-inactivated HCC cells. In light of these results, we believe that our statement that “Although these alterations were not found systematically in both cell lines and conditions (reflecting thus presumably their distinct differentiation grade and plectin inactivation efficacy), collectively these data confirmed plectin-dependent adhesome remodeling together with attenuation of oncogenic FAK, MAPK/Erk, and PI3K/Akt pathways upon plectin inactivation” (see pages 8-9) is fully supported. Furthermore, in support of the results of MS-based (phospho)proteomic and immunoblot analyses we show strong correlation between plectin expression and the signatures of “Integrin pathway” (R²=0.15, p= 2x10^-45), “FAK pathway” (R²=0.11, p= 2x10^-34), “PI3K Akt/mTOR signaling” (R²=0.06, p= 2x10^-20) or “Erk pathway” (R²=0.10, p= 6x10^-30) in HCC samples from 1268 patients (Fig S7-2C and S7-3).

In conclusion, we show that plectin is required for proper/physiological adhesion-associated signaling pathways in HCC cells. The HCC adhesome and associated pathways are dysregulated upon plectin inactivation and we show context-dependent varying degrees of attenuation of the FAK, MAPK/Erk, and PI3K/Akt pathways. In our view, presenting context-dependent variability in expression/activation of pathway molecular denominators is a trade-off for our intention to address this aspect of plectin inactivation in the complexity of different cell lines, tissues, and modes of inactivation. We prefer rather this complex approach to presenting “more convincing” black-and-white data assessed in a single cell line (Qi et al., 2022) or upon plectin inactivation by a single approach (compare with otherwise excellent studies such as (Xu et al., 2022) or (Buckup et al., 2021)). In fact, unlike the reviewers, we consider this complexity (and the resulting heterogeneity of the data) to be a strength rather than a weakness of our study.

Reviewer 1:

(1) The authors suggest that plectin controls oncogenic FAK, MAPK/Erk, and PI3K/Akt signaling in HCC cells, representing the mechanisms by which plectin promotes HCC formation and progression. However, the effect of plectin inactivation on these signaling was inconsistent in Huh7 and SNU-475 cells (Figure 3D), despite similar cell growth inhibition in both cell lines (Figure 2G). For example, pAKT and pERK were only reduced by plectin inhibition in SNU-475 cells but not in Huh7 cells.

We agree with the reviewer that plectin inactivation yields varying degrees of attenuation of the FAK, MAPK/Erk, and PI3K/Akt pathways depending on the cell type (Huh7 vs SNU-475 cells) and mode of plectin inactivation (CRISPR/Cas9-generated plectin KO vs functional KO (∆IFBD) vs organorutheniumbased inhibitor plecstatin-1). This context-dependent heterogeneity in the expression/activation of molecular denominators of signaling pathways reflects different degrees of cytoskeletal (e.g. #ventral stress fibers, Fig 4A,D and vimentin architecture, Fig S4A-C) and focal adhesion (e.g. %central FA, Fig 4A,E) phenotypes under different conditions. We expect, that functional consequences (such as reduced migration and anchorage-independent proliferation) arise from a combination of changes in individual pathways. The sum of often subtle changes will result in comparable effects not only on cell growth, but also on migration or transmission of traction forces. For more detailed comment, please see our response to all Reviewers on the first three pages of this letter.

We believe, that our data show that both pAkt and pErk are attenuated upon plectin inactivation in both Huh7 and SNU-475 cells. The following data (shown in Figs 3D and S3C) are expressed as a percentage of untreated WT, with downregulated values are highlighted in red:

Author response table 2.

(2) In addition, pFAK was not changed by plectin inhibition in both cells, and the ratio of pFAK/FAK was increased in both cells.

We agree with the reviewer that pFAK/FAK levels are either comparable or slightly higher upon plectin inactivation. However, we believe that our data convincingly show that FAK expression is downregulated in both Huh7 and Snu-475 cells. In our opinion, this results in an overall attenuation of the FAK signaling (see percentage for Normalized pFAKxNormalized FAK), which is expectedly more pronounced in migratory Snu-475 cells. The following data (shown in Figs 3D and S3C) are expressed as a percentage of untreated WT, with downregulated values are highlighted in red:

Author response table 3.

Given these results, we feel that our statement that “inhibition of plectin attenuates FAK signaling” (pages 8-9) is well supported.

(3) Thus, it is hard to convince me that plectin promotes HCC formation and progression by regulating these signalings.

Previous studies have shown that dysregulation of cell adhesions and attenuation of adhesionassociated FAK, MAPK/Erk, and PI3K/Akt signaling has inhibitory effects on HCC formation and progression. We show that plectin is required for the proper/physiological functioning of adhesionassociated signaling pathways in selected HCC cells. The HCC adhesome and associated pathways are dysregulated upon plectin inactivation and we show context-dependent varying degrees of attenuation of the FAK, MAPK/Erk, and PI3K/Akt pathways. We support these conclusions by providing the reader with proteomic and phosphoproteomic comparisons of adhesion-associated signaling between WT and plectin-inactivated HCC cell lines (Figs 3B,C and S3A,B). We further validate our findings by extensive and quantitative immunoblotting analysis (Figs 3D and S3C). In addition, we show a strong correlation between plectin expression and the signatures of “Integrin pathway” (R²=0.15, p= 2x10^-45), “FAK pathway” (R²=0.11, p= 2x10^-34), “PI3K Akt/mTOR signaling” (R²=0.06, p= 2x10^-20) or “Erk pathway” (R²=0.10, p= 6x10^-30) in HCC samples from 1268 patients (Fig S7E).

Our data and conclusions are fully consistent with previously published studies in HCC cells. For instance, even a mild decrease in FAK levels leads to a significant reduction in colony size (see effects of KD (Gnani et al., 2017) , effects of FAK inhibitor and sorafenib in xenografts (Romito et al., 2021), or effects of inhibitors in soft agars and xenografts (Wang et al., 2016)). Similar effects were observed upon partial Akt inhibition (compare with Akt inhibitors in soft agars (Cuconati et al., 2013; Liu et al., 2020)). Of course, we cannot rule out synergistic plectin-dependent effects mediated via adhesion-independent mechanisms. To identify these mechanisms and to distinguish contribution of various consequences of cytoskeletal dysregulation to phenotypes described in this manuscript would be experimentally challenging and we feel that these studies go beyond the scope of our current study.

As we feel that the adhesion-independent mechanisms were not sufficiently discussed in the original manuscript, we have removed the original sentence “Given the well-established oncogenic activation of these pathways in human cancer(33), our study identifies a new set of potential therapeutic targets.” (page 15) from the Discussion and added the following text: “However, it is conceivable that dysregulated cytoskeletal crosstalk could affect HCC through multiple mechanisms independent from FA-associated signaling. Indeed, we and others (Jirouskova et al., 2018; Xu et al., 2022) have shown that upon plectin inactivation, liver cells acquire epithelial characteristics that promote increased intercellular cohesion and reduced migration. Further studies will be required to identify and investigate synergistic adhesion-independent effects of plectin inactivation on HCC growth and metastasis.” (page 15). See also our response to Reviewer 2, #4 and Reviewer 3, #3 and #4.

(4) The authors claimed that Plectin inactivation inhibits HCC invasion and metastasis using in vitro and in vivo models. However, the results from in vivo models were not as compelling as the in vitro data. The lung colonization assay is not an ideal in vivo model for studying HCC metastasis and invasion, especially when Plectin inhibition suppresses HCC cell growth and survival. Using an orthotopic model that can metastasize into the lung or spleen could be much more convincing for an essential claim.

We agree with the reviewer that the orthotopic in vivo model would be an ideal setting to address HCC metastasis experimentally. There are several published models of HCC extrahepatic metastasis, including an orthotopic model of lung metastasis (Fan et al., 2012; Voisin et al., 2024; You et al., 2016), but to our knowledge, none of these orthotopic models are commonly used in the field. In contrast, the administration of tumor cells via the tail vein of mice is a standard, well-established approach of first choice for modelling lung metastasis in a variety of tumor types (e.g. (Hiratsuka et al., 2011; Jakab et al., 2024; Lu et al., 2020)), including HCC (Jin et al., 2017; Lu et al., 2020; Tao et al., 2015; Zhao et al., 2020). 

Furthermore, we do not believe that the use of an orthotopic model would provide a comparable advantage in terms of plectin-mediated effects on metastatic growth compared to tail vein delivery of tumor cells. Importantly, the lung colonization model used in our study allows for the injection of a defined number of HCC cells into the bloodstream, thus eliminating the effect of the primary tumor size on the number of metastasizing cells. To distinguish between effects of plectin inhibition on HCC cell growth/survival and dissemination, we carefully evaluated both the number and volume of lung metastases (Figs 6I and S6C-F). The observed reduction in the number of metastases (Figs 6I and S6D) reflects the initiation/early phase of metastasis formation, which is strongly influenced by the adhesion, migration, and invasion properties of the HCC cells and corresponds well with the phenotypes described after plectin inactivation in vitro (Figs 4H,I; 5; 6A-E; S5; and S6A,B). The reduction in the volume of metastases (Figs 6I and S6E) reflects the effects of plectin inhibition on HCC cell growth and metastatic outgrowth and corresponds well with the in vitro data shown in Figs 2G,H and S2F,G.

(5) Also, in Figure 6H, histology images of lungs from this experiment need to be shown to understand plectin's effect on metastasis better.

We are grateful to the reviewer for bringing our attention to the lung colonization assay results presented. The description of the experiments in the text of the original manuscript was incorrect. The animals monitored by in vivo bioluminescence imaging (shown in Fig 6H) are the same as the mice from which cleared whole lung lobes were analyzed by lattice light sheet fluorescence microscopy (shown in Fig. 6I). The corrected description is now provided in the revised manuscript as follows: “To identify early phase of metastasis formation, we next monitored the HCC cell retention in the lungs using in vivo bioluminescence imaging (Fig. 6H). This experimental cohort was expanded for WT-injected mice which were administered PST…” (page 11).

Therefore, lungs from all animals shown in Fig 6H,I were CUBIC-cleared and analyzed by lattice light sheet fluorescence microscopy. As requested by Reviewer 2, Recommendation #1, we provide in the revised manuscript (Fig S6F) “whole slide scan results for all the groups” which could help to understand plectin's effect on metastasis better”. To address the reviewer's concern, we also post-processed cleared and visualized lungs for hematoxylin staining and immunolabeled them for HNF4α. A representative image is shown as a panel A in Author response image 1. Post-processing of CUBIC-cleared and immunolabeled lung lobes resulted in partial tissue destruction and some samples were lost. In addition, as the entire experimental setup was designed for the early phase of metastasis formation, only small Huh7 foci were formed (compared to the larger metastases that developed within 13 weeks after inoculation shown in the panel B). As the IHC for HNF4α provides significantly lower sensitivity compared to the immunofluorescence images provided in the manuscript, we were only able to identify a few HNF4α-positive foci. Overall, we consider our immunofluorescence images to be qualitatively and quantitatively superior to IHC sections. However, if the reviewer or the editor considers it beneficial, we are prepared to show our current data as a part of the manuscript.

Author response image 1.

(A) HNF4α staining of lung tissue after CUBIC clearing from mice inoculated with WT Huh7 from the timepoint of BLI, when the positive signal in chest area has been detected. This timepoint was then selected for the comparison of initial stages of lung colonization. (B) H&E and HNF4α staining from lung tissue of mice inoculated with WT Huh7 cells from the survival experiment. Scale bars, 50 µm.

(6) Figure 6G, it is unclear how many mice were used for this experiment. Did these mice die due to the tumor burdens in the lungs?

The number of animals is given in the legend to Fig 6G (page 34; N = 14 (WT), 13 (KO)). Large Huh7 metastases were identified in the lungs of animals that could be analyzed post-mortem by IHC (see panel B in the figure above). No large metastases were found in other organs examined, such as the liver, kidney and brain. It is therefore highly likely that these mice died as a result of the tumor burden in the lungs. A similar conclusion was drawn from the results of the lung colonization model in the previous studies (Jin et al., 2017; Zhao et al., 2020).

(7) The whole paper used inhibition strategies to understand the function of plectin. However, the expression of plectin in Huh7 cells is low (Figure 1D). It might be more appropriate to overexpress plectin in this cell line or others with low plectin expression to examine the effect on HCC cell growth and migration.

For this study, we selected two model HCC cell lines – Huh7 and SNU-475. Our intention was to investigate the role of plectin in “well-differentiated” (Huh7) and “poorly differentiated” (SNU-475) HCC cells, including thus early and advanced stages of HCC development (as categorized before (Boyault et al., 2007; Yuzugullu et al., 2009a); see also our description and rationale on page 6). As anticipated, less migratory “epithelial-like” Huh7 cells are characterized by relatively high E-cadherin, low vimentin, and low plectin expression levels (Fig 1D). In contrast, migratory “mesenchymal-like” SNU-475 cells are characterized by relatively low E-cadherin, high vimentin, and high plectin expression levels (Fig 1D). Therefore, the majority of analyses were performed in both relatively low plectin-expressing Huh7 and high plectin-expressing SNU-475 cells. It is noteworthy, that inactivation of plectin had similar (although less pronounced) inhibitory effects on growth and migration in both Huh7 and SNU-475 cells.

We agree with the reviewer that “It might be more appropriate to overexpress plectin in this cell line or others with low plectin expression to examine the effect on HCC cell growth and migration”. In fact, we have received similar suggestions since we started publishing our studies on plectin. There are two reasons, which preclude the successful overexpression experiments. First, there are about 14 known isoforms of plectin (Prechova et al., 2023). Although, previous studies have analyzed the phenotypic rescue potential of some plectin isoforms using transient transfection (e.g. (Burgstaller et al., 2010; Osmanagic-Myers et al., 2015; Prechova et al., 2022)), the isoform variability precludes rescue/overexpression experiments if the causative isoform is not known. Second, plectin is a giant cytoskeletal crosslinker protein of more than 4,500 amino acids with binding sites for intermediate filaments, F-actin, and microtubules. Overexpression of the approximately 500 kDa-large crosslinker invariably leads to the collapse of cytoskeletal networks in every cell type we have tested so far. See also our response to Reviewer 3, #2.

Reviewer 2:

(1) The annotation of mouse numbers is confusing. In Figures 2A B D E F, it should be the same experiment, but the N numbers in A are 6 and 5. In E and F they are 8 and 3. Similarly, in Figure 2H, in the tumor size curve, the N values are 4,4,5,6. In the table, N values are 8,8,10,11 (the authors showed 8,7,8,7 tumors that formed in the picture). 

We are grateful to the reviewer for bringing our attention to the inconsistency the number of animals in DEN-induced hepatocarcinogenesis. Results from two independent cohorts are presented in the manuscript. The first cohort was used for MRI screening (Fig 2A-C) and at the second screening timepoint of 44 weeks, approximately 75% of animals died during anesthesia. Therefore, the second cohort of Ple^ΔAlb and Ple^fl/fl mice was used for macroscopic confirmation and histology (Figs 2D-F and S2A). We agree with the reviewer that the original presentation of the data may be misleading; therefore, we have rephrased the sentence describing macroscopic confirmation and histology (Figs 2D-F and S2A) as follows: “Decreased tumor burden in the second cohort of Ple^ΔAlb mice was confirmed macroscopically…” (page 7).

For the experiments shown in Fig 2H, mice were injected in both hind flanks. We have added this information to the figure legend along with the correct number of tumors.

(2) In Figure 3D and Figure S3C, the changes in most of the proteins/phosphorylation sites are not convincing/consistent. These data are not essential for the conclusion of the paper and WB is semi-quantitative. Maybe including more plots of the proteins from proteomic data could strengthen their detailed conclusions about the link between Plectin and the FAK, MAPK/Erk, PI3K/Akt pathways as shown in 3E.

We agree with the reviewer that plectin inactivation yields varying degrees of attenuation of the FAK, MAPK/Erk, and PI3K/Akt pathways depending on the cell type (Huh7 vs SNU-475 cells) and mode of plectin inactivation (CRISPR/Cas9-generated plectin KO vs functional KO (∆IFBD) vs organorutheniumbased inhibitor plecstatin-1). This context-dependent heterogeneity in the expression/activation of pathway molecular denominators reflects different degrees of cytoskeletal (e.g. #ventral stress fibers, Fig 4A,D and vimentin architecture, Fig S4A-C) and focal adhesion (e.g. %central FA, Fig 4A,E) phenotypes under different conditions. See also the detailed response to all reviewers (on the first three pages of this letter) and the responses to Reviewer 1, #1 and #2, Reviewer 3, #4.

Our immunoblot analysis is based on NIR fluorescent secondary antibodies which were detected and quantified using an Odyssey imaging system (LI-COR Biosciences). This approach allows a wider linear detection range than chemiluminescence without a signal loss and is considered to provide quantitative immunoblot detection (Mathews et al., 2009; Pillai-Kastoori et al., 2020) (see also manufacturer's website: https://www.licor.com/bio/applications/quantitative-western-blots/).

Following the reviewer's recommendation, we have carefully reviewed our proteomic and phosphoproteomic data. There are no further MS-based data (other than those already presented in the manuscript) to support the association of plectin with the FAK, MAPK/Erk, PI3K/Akt pathways.

(3) Figure S7A and B, The pictures do not show any tumor, which is different from Figure 7A and B (and from the quantification in S7A lower right). Is it just because male mice were used in Figure 7 and female mice were used in Figure S7? Is there literature supporting the sex difference for the Myc-sgP53 model?

As indicated in the Figure legends and in the corresponding text in the Results section (page 12), the Fig 7A,B shows Myc;sgTp53-driven hepatocarcinogenesis in male mice, whereas Fig S7C,D shows results from the female cohort. In general, the HDTVi-induced HCC onset and progression differs considerably between individual experiments, and it is therefore crucial to compare data within an experimental cohort (as we have done for Ple^ΔAlb and Ple^fl/fl mice). Nevertheless, we cannot exclude the influence of sexual dimorphism on the results presented. The existence of sexual dimorphism in liver cancer is supported by a substantial body of evidence derived from various studies (e.g. (Bigsby and CaperellGrant, 2011; Bray et al., 2024)). To date, no reports have specifically addressed sexual dimorphism in Myc;sgTp53 HDTVI-induced liver cancer. This is likely due to the fact that the vast majority of studies using this model have only presented data for one sex. However, a study using an HDTVI-administered combination of c-MET and mutated beta-catenin oncogenes to induce HCC in mice observed elevated levels of alpha-fetoprotein (AFP) in males when compared to females (Bernal et al., 2024). The study suggests that estrogen may have a protective effect in female mice, as ovariectomized females had AFP levels comparable to those observed in males. Our data suggest that female hormones may have a similar effect in the Myc;sgTp53 HDTVI-induced liver cancer model.

(4) Figure 2F, S2A, Ple^ΔAlb mice more frequently formed larger tumors, as reflected by overall tumor size increase. The interpretation of the authors is "possibly implying reduced migration or increased cohesion of plectin-depleted cells". It is quite arbitrary to make this suggestion in the absence of substantial data or literature to support this theory.

We agree with the reviewer that our statement “Notably, Ple^ΔAlb mice more frequently formed larger tumors, as reflected by overall tumor size increase (Fig. 2F; Figure 2—figure supplement 1A), possibly implying reduced migration or increased cohesion of plectin-depleted cells(25).” (page 7) is rather speculative. As we did not further address the formation of larger tumors in Ple^ΔAlb mice further in the current study, we wanted to provide the readers with some, even speculative, hypotheses. In support of our hypothesis, we cite our own publication (#26; Jirouskova et al., J Hepatol., 2018), where we show that plectin inactivation in Ple^ΔAlb livers results in upregulation of the epithelial marker E-cadherin. Previous studies have shown that similar increase in E-cadherin expression levels reflects mesenchymalto-epithelial transition (e.g. (Adhikary et al., 2014; Auersperg et al., 1999; Wendt et al., 2011)) and is often associated with reduced cancer cell migration/invasion. This is consistent with our finding that “migrating plectin-disabled SNU-475 cells exhibited more cohesive, epithelial-like features while progressing collectively. By contrast, WT SNU-475 leader cells were more polarized and found to migrate into scratch areas more frequently than their plectin-deficient counterparts (Figure 5—figure supplement 1B). Consistent with this observation, individually seeded SNU-475 cells less frequently assumed a polarized, mesenchymal-like shape upon plectin inactivation in both 2D and 3D environments (Fig. 5C). Moreover, plectin-inactivated SNU-475 cells exhibited a decrease in N-cadherin and vimentin levels when compared to WT counterparts (Figure 5—figure supplement 1C).” (page 10).

In conclusion, we have shown that plectin-deficient hepatocytes express higher levels of E-cadherin and hepatocyte-derived SNU-475 cells express less N-cadherin and vimentin. In addition, we show that SNU475 cells exhibited more cohesive, epithelial-like features in scratch-wound experiments. To address the reviewer's concern and to further support our statement about the increased cohesiveness of plectindeficient HCC cells we have included the citation of the recent study #27 (Xu et al., 2022). Using the MHCC97H and MHCC97L HCC cell lines, this study shows that plectin downregulation “inhibits HCC cell migration and epithelial mesenchymal transformation”, which is fully consistent with our hypothesis. To mitigate the impression of an unsubstantiated statement, we also discuss adhesion-independent plectin-mediated mechanisms in the revised Discussion section as follows: “However, it is conceivable that dysregulated cytoskeletal crosstalk could affect HCC through multiple mechanisms independent from FA-associated signaling. Indeed, we and others (Jirouskova et al., 2018; Xu et al., 2022) have shown that upon plectin inactivation, liver cells acquire epithelial characteristics that promote increased intercellular cohesion and reduced migration. Further studies will be required to identify and investigate synergistic adhesion-independent effects of plectin inactivation on HCC growth and metastasis.” (page 15).

(5) Mutation or KO PLEC has been shown to cause severe diseases in humans and mice, including skin blistering, muscular dystrophy, and progressive familial intrahepatic cholestasis. Please elaborate on the potential side effects of targeting Plectin to treat HCC.

Indeed, mutation or ablation of plectin has been implicated in many diseases (collectively known as plectinopathies). These multisystem disorders include an autosomal dominant form of epidermolysis bullosa simplex (EBS), limb-girdle muscular dystrophy, aplasia cutis congenita, and an autosomal recessive form of EBS that may be associated with muscular dystrophy, pyloric atresia, and/or congenital myasthenic syndrome. Several mutations have also been associated with cardiomyopathy and malignant arrhythmias. Progressive familial intrahepatic cholestasis has also been reported. In genetic mouse models, loss of plectin leads to skin fragility, extensive intestinal lesions, instability of the biliary epithelium, and progressive muscle wasting (for more details see (Vahidnezhad et al., 2022)). 

It is therefore important to evaluate potential side effects, and plectin inactivation therefore presents challenges comparable to other anti-HCC targets. For instance, Sorafenib, the most widely used chemotherapy in recent decades, targets numerous serine/threonine and tyrosine kinases (RAF1, BRAF, VEGFR 1, 2, 3, PDGFR, KIT, FLT3, FGFR1, and RET) that are critical for proper non-pathological functions (Strumberg et al., 2007; Wilhelm et al., 2006; Wilhelm et al., 2004). The combinatorial therapy of atezolizumab and bevacizumab targets also PD-L1 in conjunction with VEGF, which plays an essential role in bone formation (Gerber et al., 1999), hematopoiesis (Ferrara et al., 1996), or wound healing (Chintalgattu et al., 2003). To allow readers to read a comprehensive account of the pathological consequences of plectin inactivation, we included two additional citations (Prechova et al., 2023; Vahidnezhad et al., 2022)  and rephrased Introduction section as follows: “…multiple reports have linked plectin with tumor malignancy(12) and other pathologies (Prechova et al., 2023; Vahidnezhad et al., 2022), mechanistic insights…” (page 4-5).

Reviewer 3:

(1) The rationale for using Huh7 cells in the manuscript is not well explained as it has the lowest Plectin expression levels.

For this study, we selected two model HCC cell lines - Huh7 and SNU-475. Our intention was to address the role of plectin in “well-differentiated” (Huh7) and “poorly differentiated” (SNU-475) HCC cells, thus including early and advanced stages of HCC development (as categorized before (Boyault et al., 2007; Yuzugullu et al., 2009b) see also our description and reasoning on page 6). The Huh7 cell line is also a well-established and widely used model suitable for both in vitro and in vivo settings (e.g. (Du et al., 2024; Fu et al., 2018; Si et al., 2023; Zheng et al., 2018).

As anticipated, less migratory “epithelial-like” Huh7 cells are characterized by relatively high E-cadherin, low vimentin, and low plectin expression levels (Fig 1D). In contrast, migratory “mesenchymal-like” SNU475 cells are characterized by relatively low E-cadherin, high vimentin, and high plectin expression levels (Fig 1D). Therefore, the majority of analyses were performed in both relatively low plectin-expressing Huh7 and high plectin-expressing SNU-475 cells. It is noteworthy, that inactivation of plectin had similar (although less pronounced) inhibitory effects on the phenotypes in both Huh7 and SNU-475 cells. We believe that these findings highlight the importance of plectin in HCC growth and metastasis, as plectin inactivation has inhibitory effects on both early (low plectin) and advanced (high plectin) stages of HCC.

(2) The KO cell experiments should be supplemented with overexpression experiments.

We agree with the reviewer that it would be helpful to complement our plectin inactivation experiments by overexpressing plectin in the HCC cell lines used in this study. In fact, we have received similar suggestions since we started to publish our studies on plectin. There are two reasons, which preclude the successful overexpression experiments. First, there is about 14 known isoforms of plectin (Prechova et al., 2023). Although previous studies have analyzed the phenotypic rescue potential of some plectin isoforms using transient transfection (e.g. (Burgstaller et al., 2010; Osmanagic-Myers et al., 2015; Prechova et al., 2022)), the isoform variability precludes rescue/overexpression experiments if the causative isoform is not known. Second, plectin is a giant cytoskeletal crosslinker protein of more than 4,500 amino acids with binding sites for intermediate filaments, F-actin, and microtubules. Overexpression of the approximately 500 kDa-large crosslinker invariably leads to the collapse of cytoskeletal networks in every cell type we have tested so far. See also our response to Reviewer 1, #7.

(3) There is significant concern that while ablation of Ple led to reduced tumor number, these mice had larger tumors. The data indicate that Plectin may have distinct roles in HCC initiation versus progression. The data are not well explained and do not fully support that Plectin promotes hepatocarcinogenesis.

In the DEN-induced HCC model MRI screening revealed fewer tumors and also tumor volume was reduced at 32 and 44 weeks post-induction (Fig 2A-C). Larger tumors formed in Ple^ΔAlb compared to Ple^fl/fl livers (Figs 2F and S2A) refer only to a subset of macroscopic tumors visually identified at necropsy. Larger Ple^ΔAlb tumors were not observed in the Myc;sgTp53 HDTVI-induced HCC model (data not shown). In contrast, plectin deficiency reduced the size of xenografts formed in NSG mice (Fig 2H), and agar colonies grown from Huh7 and SNU-475 cells with inactivated plectin were also smaller (Fig S2F). In all in vivo and in vitro approaches presented in the manuscript, plectin inactivation reduced the number of colonies/xenografts/tumors. As hepatocarcinogenesis is a multistep process including initiation, promotion, and progression (Pitot, 2001), we feel confident in concluding that plectin inactivation inhibits hepatocarcinogenesis and we consider this conclusion to be fully supported by the data presented in the manuscript.

However, we agree with the reviewer that larger macroscopic Ple^ΔAlb tumors in the DEN-induced HCC model are intriguing. As we do not see similar effects (or even trends) in other approaches used in this study, we cannot exclude the contribution of plectin-deficient environment in Ple^ΔAlb livers during longterm (44 weeks) tumor formation and growth. In our previous study (Jirouskova et al., 2018), we showed that plectin deficiency in Ple^ΔAlb livers leads to biliary tree malformations, collapse of bile ducts and ductules, and mild ductular reaction. We could speculate that Ple^ΔAlb livers suffer from continuous bile leakage into the parenchyma, which would exacerbate all models of long-term pathology.

As we did not further address the formation of larger tumors in Ple^ΔAlb mice further in the current study, we offered the reader the hypothesis that large tumors could “…possibly implying reduced migration or increased cohesion of plectin-depleted cells25.” In support of our hypothesis, we cite our own publication (#26; Jirouskova et al., J Hepatol., 2018), where we show that plectin inactivation in Ple^ΔAlb livers results in upregulation of the epithelial marker E-cadherin. Previous studies have shown that similar increase in E-cadherin expression levels reflects mesenchymal-to-epithelial transition (e.g. (Adhikary et al., 2014; Auersperg et al., 1999; Wendt et al., 2011)) and is often associated with reduced cancer cell migration/invasion. This is consistent with our finding that “migrating plectin-disabled SNU475 cells exhibited more cohesive, epithelial-like features while progressing collectively. By contrast, WT SNU-475 leader cells were more polarized and found to migrate into scratch areas more frequently than their plectin-deficient counterparts (Figure 5—figure supplement 1B). Consistent with this observation, individually seeded SNU-475 cells less frequently assumed a polarized, mesenchymal-like shape upon plectin inactivation in both 2D and 3D environments (Fig. 5C). Moreover, plectin-inactivated SNU-475 cells exhibited a decrease in N-cadherin and vimentin levels when compared to WT counterparts (Figure 5—figure supplement 1C).” (page 10).

In conclusion, we have shown that plectin-deficient hepatocytes express higher levels of E-cadherin and hepatocyte-derived SNU-475 cells less N-cadherin and vimentin. In addition, we show that SNU-475 cells exhibited more cohesive, epithelial-like features in scratch-wound experiments. To address the reviewer's concern and to further support our claim of increased cohesiveness of plectin-deficient HCC cells we included the citation of the recent study(27). Using the MHCC97H and MHCC97L HCC cell lines, this study shows that plectin downregulation “inhibits HCC cell migration and epithelial mesenchymal transformation” and is therefore fully consistent with our hypothesis. To mitigate the impression of an unsubstantiated statement, we also discuss adhesion-independent plectin-mediated mechanisms in the revised Discussion section as follows: “However, it is conceivable that dysregulated cytoskeletal crosstalk could affect HCC through multiple mechanisms independent from FA-associated signaling. Indeed, we and others (Jirouskova et al., 2018; Xu et al., 2022) have shown that upon plectin inactivation, liver cells acquire epithelial characteristics that promote increased intercellular cohesion and reduced migration. Further studies will be required to identify and investigate synergistic adhesionindependent effects of plectin inactivation on HCC growth and metastasis.” (page 15).

(4) Figure 3 showed that Plectin does not regulate p-FAK/FAK expression. Therefore, the statement that Plectin regulates the FAK pathway is not valid. Furthermore, there are too many variables in turns of p-AKT and p-ERK expression, making the conclusion not well supported.

We agree with the reviewer that pFAK/FAK levels are either comparable or slightly higher upon plectin inactivation. However, we believe that our data convincingly show that FAK expression is downregulated in both Huh7 and Snu-475 cells. In our opinion, this results in an overall attenuation of the FAK signaling (see percentage for Normalized pFAKxNormalized FAK), which is expectedly more pronounced in migratory Snu-475 cells. The following data (shown in Figs 3D and S3C) are expressed as a percentage of untreated WT, with downregulated values highlighted in red:

Author response table 4.

Given these results, we believe that our statement that “inhibition of plectin attenuates FAK signaling” (pages 8-9) is well supported.

We believe, that our data show that both pAkt and pErk are attenuated upon plectin inactivation in both Huh7 and SNU-475 cells. The following data (presented in Figs 3D and S3C) are shown as a percentage of untreated WT, with downregulated values highlighted in red:

Author response table 5.

We agree with the reviewer that plectin inactivation yields varying degrees of attenuation of the FAK, MAPK/Erk, and PI3K/Akt pathways depending on the cell type (Huh7 vs SNU-475 cells) and mode of plectin inactivation (CRISPR/Cas9-generated plectin KO vs functional KO (∆IFBD) vs organorutheniumbased inhibitor plecstatin-1). This context-dependent heterogeneity in the expression/activation of pathway molecular denominators reflects different degrees of cytoskeletal (e.g. #ventral stress fibers, Fig 4A,D and vimentin architecture, Fig S4A-C) and focal adhesion (e.g. %central FA, Fig 4A,E) phenotypes under different conditions. See also the detailed response to all Reviewers (on the first three pages of this letter) and the responses to Reviewer 1, #1 and #2 and Reviewer 2, #4.

(5) The studies of plecstatin-1 in HCC should be expanded to a panel of human HCC cells with various Plectin expression levels in turns of cell growth and cell migration. The IC50 values should be determined and correlate with Plectin expression.

Following the reviewer's suggestion, we have included graphs showing IC50 values for Huh7 (low plectin) and SNU-475 (high plectin) cells as Fig S2E. As expected, the IC50 values are higher for SNU-475 cells. Corresponding parts of the Figure legends have been changed. We refer to new data in the Results section as follows: “If not stated otherwise, we applied PST in the final concentration of 8 µM, which corresponds to the 25% of IC50 for Huh7 cells (Figure 2—figure supplement 1E).” (page 7). We also provide details of the IC50 determination in the revised Supplement Materials and methods section (pages 5-6).

(6) One of the major issues is the mechanistic studies focusing on Plectin regulating HCC migration/metastasis, whereas the in vivo mouse studies focus on HCC formation (Figures 3 and 7). These are distinct processes and should not be mixed.

In our study, we investigated the role of plectin in the development and dissemination of HCC. Using DEN- and Myc;sgTp53 HDTVI-induced HCC models (Figs 2A-F, S2A, 7A-C, and S7A-D), we show the effects of plectin inactivation on HCC formation in vivo. These studies are complemented by xenografts (Figs 2H and S2G) and in vitro colony formation assay (Figs 2G and S2F). Using an in vivo lung colonization assay (Figs 6G-I and S6C-F), we show the effects of plectin inactivation on the metastatic potential of HCC cells. In complementary in vitro studies, we show how plectin deficiency affects migration (Figs 5 and S5) and invasion (Figs 6A-E and S6A,B). 

Our mechanistic studies show that plectin inactivation leads to dysregulation of cytoskeletal networks, adhesions, and adhesion-associated signaling. We believe that we have provided substantial experimental data suggesting that the proposed mechanisms play a role in plectin-mediated inhibition of both HCC development and dissemination. Of course, we cannot rule out additional, adhesionindependent mechanisms for HCC formation. To clarify this, we have revised the Discussion section as follows: “However, it is conceivable that dysregulated cytoskeletal crosstalk could affect HCC through multiple mechanisms independent from FA-associated signaling. Indeed, we and others (Jirouskova et al., 2018; Xu et al., 2022) have shown that upon plectin inactivation, liver cells acquire epithelial characteristics that promote increased intercellular cohesion and reduced migration. Further studies will be required to identify and investigate synergistic adhesion-independent effects of plectin inactivation on HCC growth and metastasis.” (page 15).

(7) Figure 7B showed that Ple KO mice were treated with PST, but the data are not presented in the manuscript. Tumor cell proliferation and apoptosis rates should be analyzed as well.

We do not show any effects of PST in Ple^ΔAlb mice. As stated in the Fig 7B legend: “Myc;sgTp53 HCC was induced in Ple^fl/fl, Ple^ΔAlb, and PST-treated Ple^fl/fl (Ple^fl/fl+PST) male mice as in (A). Shown are representative images of Ple^fl/fl, Ple^ΔAlb, and Ple^fl/fl+PST livers from mice with fully developed multifocal HCC sacrificed 6 weeks post-induction.”.

Following the reviewer's recommendation, we include the analysis of proliferation and apoptosis rates as revised Fig S7A,B. Please note, that no differences in apoptosis and proliferation rates were found between experimental conditions. Due to additional data, the original Fig S7 – 1 has been split into revised Fig S7 – 1 and Fig S7 – 2.

(8) The status of FAK, AKT, and ERK pathway activation was not analyzed in mouse liver samples. In Figure 7D, most of the adjusted p-values are not significant.

We are aware that the majority of FDR corrected p-values shown in the Fig 7D are not significant. In fact, we deliberated with our colleagues from the laboratory of Prof. Samuel Meier-Menches (Department of Analytical Chemistry, University of Vienna), who conducted all the proteomic studies presented in this manuscript, on whether to present such "weak" data. Following a lengthy discussion, a decision was taken to include them despite the anticipation of criticism from the reviewers. The rationale for including these data is that, despite the lack of statistical significance, the findings are consistent with those of MS/immunoblot analyses of HCC cells (Figs 3 and S3) and patient data (Figs 7E, S7-2). The lack of statistical significance observed in the presented data is a consequence of the limited number of animals included in the Ple^fl/fl, Ple^ΔAlb, and PST-treated Ple^fl/fl cohorts, which has resulted in a high degree of variability in the MS results. We agree with the reviewer that the inclusion of immunoblot analysis would provide further support for our conclusions. However, we do not have any remaining liver tissue that could be analyzed.

(9) There is no evidence to support that PST is capable of overcoming therapy resistance in HCC. For example, no comparison with the current standard care was provided in the preclinical studies.

We are grateful to the reviewer for bringing our attention to the incorrect statement in the Abstract: “…we show that plectin inhibitor plecstatin-1 (PST) is well-tolerated and capable of overcoming therapy resistance in HCC”. To address the reviewer's concern, we rephrased the Abstract as follows: “…we show that plectin inhibitor plecstatin-1 (PST) is well-tolerated and potently inhibits HCC progression”.

Recommendations for the authors: 

Reviewer 2 (Recommendations for the authors):

(1) In Figures 6I and S6C, it would be better to show the whole slide scan result for all the groups.

Following the reviewer's recommendation, we include the whole slide scan result for all the groups as revised Fig S6F.

(2) In Figures S7C and D, what do the highlighted/colored dots represent? They are not mentioned in the figure legend or the results.

Following the reviewer's recommendation, we include the explanation in the revised Figure legends (page 30).

(3) In Figure 2H, the experiment schedule showed "6w Huh7 t.v.i.", but should it be subcutaneous injection?

We are grateful to the reviewer for bringing our attention to the incorrect description of the experiment. The schematics was corrected. The schematic has been corrected. We have also noticed an error in the table summarizing the number of tumors formed (N) and have corrected the values for the WT+PST and KO conditions.

(4) Supplemental Materials and Methods, Xenograft tumorigenesis, Error: 2.5×106 Huh7 cells in 250 ml PBS mice were administered subcutaneously in the left and right hind flanks. It probably should be "250ul".

We are grateful to the reviewer for bringing our attention to the incorrect description of the experiment. The corresponding part of the Materials and Methods section has been corrected (page 2).

(5) In Figure legend Supplementary Figure 6 C,D,E : "Representative magnified images from lung lobes with GFP-positive WT, KO, and WT+PST SNU-475 nodules". There is no picture for the WT+PST SNU-475 group.

We are grateful to the reviewer for bringing our attention to the incorrect description of the experiment. The corresponding part of the Figure legend (“WT+PST SNU-475”) has been deleted (page 27).

(6) In the Figure legend for Figure 6H, "Representative BLI images of WT, KO, and PST-treated WT (WT+PST) SNU-475 cells-bearing mice are shown". Should it be Huh7, not SNU-475?

We are grateful to the reviewer for bringing our attention to the incorrect description of the experiment. The description of the cell line has been corrected (page 34).

(7) The statement that current therapies rely on multikinase inhibitors is no longer correct.

We are grateful to the reviewer for bringing our attention to the incorrect statement. To address the reviewer's concern, we rephrased the original part of Discussion section: “Current therapies for HCC rely on multikinase inhibitors (such as sorafenib) that provide only moderate survival benefit(60,61) due to primary resistance and the plasticity of signaling networks(62)” as follows: “Current systemic therapies for advanced HCC rely on a combination of multikinase inhibitor (such as sorafenib) or anti-VEGF /VEGF inhibitor (such as bevacizumab) treatment with immunotherapy(59). Multikinase inhibitors provide only moderate survival benefit(60,61) due to primary resistance and the plasticity of signaling networks(62), and only a subset of patients benefits from addition of immunotherapy in HCC treatment(63)” (page 15).

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Author response:

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

Response to the Reviewer #1 (Public review):

We greatly appreciate the reviewer’s high evaluation of our paper and helpful comments. As expected, we revealed that the CCL17/CCL22–CCR4 axes play an important role in guiding Tregs to the atherosclerotic aorta. Interestingly, we also demonstrated that these axes are critical for Treg-dependent regulation of proinflammatory T cell responses in lymphoid tissues and atherosclerotic aortas, which is a previously unrecognized role for CCR4 in regulating inflammatory immune responses. However, the role of the CCL17/CCL22–CCR4 axes in regulating inflammatory immune responses and atherosclerosis has not been fully elucidated and further investigation is needed.

Response to the reviewer #2 (Public review):

We greatly appreciate the reviewer’s high evaluation of our paper and helpful comments and suggestions. We isolated CD4⁺CD25⁺ T cells and used them as Tregs in several experiments. As the reviewer pointed out, we realize that CD4⁺CD25⁺ T cell population contains some activated effector T cells. However, in consideration of the high expression levels of the most reliable Treg marker Foxp3 in isolated CD4⁺CD25⁺ T cells determined by flow cytometry, we believe that our method for separating Tregs would be acceptable.

Regarding the role of Th17 cells in atherosclerosis, conflicting results have been reported. Therefore, it is unclear whether augmented Th17 cell immune responses contribute to accelerated atherosclerosis in Ccr4^-/-Apoe^-/- mice.

As the reviewer pointed out, it is important to consider the clinical relevance of our findings. We analyzed public database to determine if Ccr4 single nucleotide polymorphisms correlate with a higher incidence of atherosclerotic cardiovascular disease. However, no evidence supporting the clinical relevance of our findings was found.

Response to the Reviewer #3 (Public review):

We greatly appreciate the reviewer’s high evaluation of our paper and helpful comments and suggestions. In accordance with the reviewer’s suggestion, we described the detailed methods and carefully performed data analysis regarding flow cytometry, which would strengthen the conclusion of this study.

We understood the importance of reviewer’s claim that CCR4 deficiency does not shift the Th1 cell/Treg balance toward Th1 cell responses in all lymphoid tissues. CCR4 deficiency promoted the accumulation of Th1 cells but did not affect the accumulation of Tregs in the atherosclerotic aorta, which led to the shift of the Th1 cell/Treg balance toward Th1 cell responses. The frequencies of both Tregs and Th1 cells in peripheral lymphoid tissues were increased by CCR4 deficiency, while these CCR4-deficient Tregs exhibited impaired suppressive function. Given this, we speculate that CCR4 deficiency may shift the Th1 cell/Treg balance toward Th1 cell responses in peripheral lymphoid tissues. However, it is difficult to clearly show this. We revised the manuscript accordingly.

Although the reviewer pointed out the possibility that modulation of the Th1 cell/Th17 cell balance might be responsible for the changes in aortic inflammatory cells in Ccr4^-/-Apoe^-/- mice, the role of Th17 cells in atherosclerosis remain controversial. However, we cannot completely exclude the possibility of the involvement of the Th17 response modulation in accelerated atherosclerosis in Ccr4^-/-Apoe^-/- mice.

As the limitation of this study, the phenotypic heterogeneity and dynamics of aortic leukocytes could not be revealed by flow cytometric analysis. Single-cell proteomic and transcriptomic approaches would provide additional important information on various aortic cells including immune cells and vascular cells.

Reviewer #1 (Recommendations for the authors):

Issue (1) Ideally, CCR4 could be deleted on Foxp3+ cells and some staining on double positive Rorg+Foxp3+ done. On the other side, a whole gene expression of infiltrated Foxp3 and effector could be also helpful. More challenging, it would be important to see whether those CCR4-specific Trges could or not regulate effector infiltrating cells.

As the reviewer suggested, single-cell proteomic and transcriptomic approaches would be helpful to reveal the phenotypic heterogeneity and dynamics of aortic leukocytes including Tregs. Also, the use of conditional knockout mice would reveal the precise role of CCR4-expressing Tregs in regulating aortic immune cell infiltration and atherosclerosis.

Reviewer #2 (Recommendations for the authors):

Minor Suggestions:

Issue (1) In supplementary Figure 1, CCR4 expression would be better represented by dot plots rather than histograms.

We revised Supplementary Figure 1A through 1C.

Issue (2) The reduction in CD103 expression shown in Figure 2E at 8 weeks should be discussed.

In Figure 2E, we found that the expression of CD103 in peripheral LN Tregs was slightly lower in 8-week-old Ccr4^-/-Apoe^-/- mice than in age-matched Apoe^-/- mice, while there was no difference in its expression levels between 18-week-old Apoe^-/- and Ccr4^-/-Apoe^-/- mice. In addition, there was no significant difference in the mRNA expression of this molecule in splenic Tregs between 8-week-old Apoe^-/- and Ccr4^-/-Apoe^-/- mice. Based on the minor effect of CCR4 deficiency on CD103 expression in Tregs, reduced CD103 expression in Ccr4^-/-Apoe^-/- mice does not seem to be an important change.

Issue (3) The increased expression of CD86 by DCs should be discussed.

The upregulated CD86 expression on DCs in Ccr4^-/-Apoe^-/- mice might be explained by the data on a Treg-DC coculture experiment showing the impaired cell–cell contacts between CCR4-deficient Tregs and DCs. On the other hand, the expression of another important costimulatory molecule CD80 on DCs was not altered in these mice, which is not consistent with the data on the above coculture experiment. The reason why only CD86 expression on DCs was upregulated in Ccr4^-/-Apoe^-/- mice remains unclear.

Issue (4) In Figures 5F-H, using larger dots would enhance visibility.

We revised the graphs in Figure 5F-H.

Issue (5) In Figure 5I, since the data is normalized, a one-sample t-test is more appropriate.

In accordance with the reviewer’s suggestion, we reconsidered the data analysis. Because there was a dramatic difference in the absolute number of Kaede-expressing Tregs accumulated in the aorta among experiments, we were worried that the statistical analysis of the combined data from multiple experiments might draw a wrong conclusion. We have decided to show the representative data from 3 independent experiments in Figure 5I.

Issue (6) On page 11, line 256, the text mentions IL4 and IL10 being detected by cytokine array; however, the figures do not show these cytokines.

We are afraid that the reviewer might have misunderstood the data. The cytokine levels of IL-4 and IL-10 could not be detected by cytokine array analysis. Accordingly, we carefully revised the text in the manuscript.

Issue (7). On page 14, lines 326-330, the text should be revised for clarity.

We revised the text in the manuscript.

Issue (8) Several data are marked as "not shown"; some of this information is relevant and should be included in the supplementary figures.

We showed the data on CCL17 and CCL22 expression in peripheral LNs in Supplementary Figure 2.

Major Suggestions:

Issue (1) FoxP3 expression should be evaluated post-isolation of CD4⁺CD25⁺ T cells, and FoxP3- CD4⁺CD25⁺ T cells should be characterized. Tregs could be more effectively isolated using FoxP3eGFP mice.

After isolation of CD4⁺CD25⁺ T cells (the purity was >95%), we examined Foxp3 expression by flow cytometry and found that most of these cells express Foxp3 (Supplementary Figure 10). Therefore, CD4⁺CD25⁺ T cells without Foxp3 expression, which are considered contaminated effector T cells, are minor cells and would not substantially affect the results. Nonetheless, the use of Foxp3-eGFP mice would enable us to isolate Tregs more accurately.

Issue (2) In Figure 3, it would be interesting to evaluate whether there are RORgt+Tbet+ (IL17+IFNg+) cells. These cells would be pathogenic, whereas RORgt+CD73+ cells would be non-pathogenic.

We analyzed CD4⁺ T cells producing both IL-17 and IFN-γ in the peripheral lymphoid tissues of Apoe^-/- and Ccr4^-/-Apoe^-/- mice. We found that this cell population was quite rare and that there was no significant difference its proportion between the 2 groups, suggesting the possible minor contribution of this cell population to the atherosclerosis phenotype.

Author response image 1.

Issue (3) Different time points after adoptive cell transfer should be evaluated to confirm reduced migration to the atherosclerotic aorta.

It would be interesting to evaluate Treg migration to the atherosclerotic aorta at different time points after Treg transfer. However, it seems difficult to accurately evaluate the migration of Tregs at later time points because they would proliferate in the aorta.

Issue (4) The authors could evaluate whether Ccr4 SNPs correlate with an increased risk of atherosclerosis.

As the reviewer pointed out, it is important to consider the clinical relevance of our findings. However, there is no evidence supporting that Ccr4 single nucleotide polymorphisms correlate with a higher incidence of atherosclerotic cardiovascular disease.

Issue (5) The authors could evaluate if the transfer of Apoe^-/- Tregs rescues early atherosclerosis development in Ccr4^-/-Apoe^-/- mice.

To confirm whether transfer of CCR4-intact Tregs rescues the development of early atherosclerotic lesions in Ccr4^-/-Apoe^-/- mice, we injected Ccr4^-/-Apoe^-/- mice with saline or Tregs from Apoe^-/- or Ccr4^-/-Apoe^-/- mice and analyzed the aortic root atherosclerotic lesions of recipient Ccr4^-/-Apoe^-/- mice. However, we found no significant difference in the aortic sinus plaque area among the 3 groups. We described this result in the results section and included the data in Supplementary Figure 8.

Reviewer #3 (Recommendations for the authors):

Analysis of TCD4⁺ cell populations in different tissues:

Issue (1) The description of flow cytometry analysis is incomplete and requires clarification. Please detail the use of controls to ensure correct analysis, including the following: i) cell viability; ii) staining controls to define positive and negative cells; iii) the gating strategy used to identify cell populations in each lymphoid tissue and aorta (please provide them as supplementary figures).

As we thought that most of the prepared cells would be viable, we did not check their viability. Based on our previous work where various immune cells including Tregs, effector memory T cells, and helper T cell subsets were clearly detected, in this study we performed flow cytometric analysis of these immune cells without preparing negative controls stained with isotype control antibodies. The gating strategy of flow cytometric analysis of various immune cells in peripheral lymphoid tissues was reported in our previous report (J Am Heart Assoc 2024; 13: e031639). We provided the gating strategy of flow cytometric analysis of helper T cells and Tregs in the aorta in Supplementary Figure 9.

Issue (2) The phenotype/differentiation markers used for analysing T CD4⁺ cell subsets differ between lymphoid tissues and aortic lesions; might this influence results? If so, please comment on that.

As the number of aortic T cells was quite few compared with that in peripheral lymphoid tissues, it seemed difficult to precisely detect aortic T cells including various helper T cell subsets and Tregs by intracellular cytokine staining. Therefore, we decided to analyze these cells by evaluating transcription factors specific for helper T cell subsets. The difference in the markers used for analyzing T cell subsets would not considerably influence the results.

Issue (3) Considering my observations about the effect of CCR4 deficiency on the T CD4⁺ differentiation profile in different tissues, I suggest comparing Th1/Treg and Th17/Treg ratios in all examined tissues. The modulation of the Th17/Th1 balance could shape inflammation.

The Th1 cell/Treg balance is shifted toward Th1 cell responses in the atherosclerotic aorta of Ccr4^-/-Apoe^-/- mice, while this balance would not be altered in the peripheral lymphoid tissues. It remains unclear whether CCR4 deficiency affects the Th17 cell/Treg ratio. We do not think that it is important to investigate the effect of CCR4 deficiency on the balance of Th17 cell/Treg or Th17 cell/Th1 cell because the role of Th17 cell responses in atherosclerosis remains controversial.

Issue (4) Cell numbers of recovered Treg from para-aortic lymphoid nodes and aortic tissues might not allow Treg functional assays. Analysis by flow cytometry of biomarkers of Treg activation state would be more informative than by quantifying mRNA expression levels. In particular, TGFβ analysis at the mRNA level does not provide much more information about the suppressive activity of Treg, and even at the protein level, the recognition of the active form of this cytokine is required. Analysis of PD1 (for exhausted cell phenotype) and Treg apoptosis along the stages of atherosclerosis could also yield useful information.

We performed flow cytometric analysis of activation markers CTLA-4 and CD103, cell exhaustion marker PD1, and apoptosis in Tregs in the para-aortic LNs of Apoe^-/- or Ccr4^-/-Apoe^-/- mice, and found no major differences in the expression levels of these molecules or the proportion of apoptotic cells between the 2 groups. We showed these data below.

Author response image 2.

Unfortunately, we failed to evaluate the activity of TGF-β in Tregs because an appropriate experimental method for precisely detecting its active form was unavailable.

Issue (5) Regarding the result´s interpretation, I recommend being precise when concluding to avoid misunderstanding. A shift in the T CD4⁺ response in lymphoid tissues might be interpreted as a modulation of the T cell differentiation process, which strongly depends on signals derived from DCs, which were not the focus of this study.

There are two possible mechanisms for the altered CD4⁺ T cell responses in peripheral lymphoid tissues, which include the modulation of their differentiation and proliferation processes. These processes are substantially regulated by DCs whose function could be favorably modulated by CCR4-expressing Tregs as described in the manuscript. Therefore, we think that the interactions between Tregs and DCs are crucial for shifting the CD4⁺ T cell responses in peripheral lymphoid tissues, though it remains unclear which process plays a major role in regulating CD4⁺ T cell polarization.

Suppression studies:

Issue (1) In vitro assays. According to the methodology suppression studies were performed using Treg collected from peripheral lymphoid nodes and spleen, but it is unclear whether these cells were analysed separately or as a pool (this was not clarified in the legend of Figure 5 either). Besides, be precise about which cells were used as antigen-presenting cells in the Treg suppression assay.

In in vitro Treg suppression assay, we used Tregs purified from peripheral lymph nodes and spleen as a pool. We used splenocytes as antigen-presenting cells in Treg suppression assay. We revised the manuscript accordingly.

Issue (2) Obtaining CD4⁺CD25⁺ and CD4⁺CD25-. The control of the purity and viability of cell preparations from CCR4 deficient and CCR4 sufficient Apoe^-/- mice should be included as a supplementary material; these purified cells were used in in vitro suppressive assays and in vivo cell transfer experiments, being relevant information to guarantee results. Since this control was performed by flow cytometry, I wonder whether Foxp3 levels were also checked.

We included the data on the purity and viability of CD4⁺CD25⁺ Tregs and CD4⁺CD25^- T cells from Apoe^-/- or Ccr4^-/-Apoe^-/- mice in Supplementary Figure 10. After the isolation of CD4⁺CD25⁺ T cells, we examined Foxp3 expression by flow cytometry and found that most of these cells express Foxp3.

Issue (3) For in vitro assays, IL-2, IL-10, and TGFβ measurement in culture supernatants could confirm and provide more information about Treg function.

As both CD4⁺CD25⁺ Tregs and CD4⁺CD25^- T cells would produce various cytokines in in vitro Treg suppression assay, it is difficult to determine which cells mainly produce the above cytokines. Therefore, measurement of these cytokines would not provide more information about Treg function.

Issue (4) It would be interesting to assess whether CCR4-mediated DC-Treg interaction is equally important to regulate Th1 than Th17 and Th2 activation; this likely requires using different settings to favour each activation profile.

Based on our findings, we speculate that CCR4 may play an important role in regulating not only Th1 cell responses but also Th2 and Th17 cell responses by maintaining the interactions between Tregs and DCs. However, it may not be meaningful to investigate the effect of CCR4 deficiency on these T cell responses because the roles of Th2 and Th17 cell responses in atherosclerosis remain controversial.

Issue (5) The authors showed that the presence of Treg decreased CD80 and CD86 surface levels in DCs in vitro, remarking a lower capacity of Treg derived from CCR4-deficient mice (Figure 5B). However, the fact that CD86 on splenic CD11c+MHC-II+ DCs in 8-week-old Ccr4^-/-Apoe^-/- mice was significantly higher than in Apoe^-/- was underestimated (Supplementary Figure 4). This data needs reconsideration as it might indicate an in vivo more permissive activation state of DCs in Ccr4^-/-Apoe^-/- mice than in Apoe^-/- mice, explaining the augmented effector T cell response observed in these mice (Figure 2).

Our finding of the upregulated CD86 expression on DCs in Ccr4^-/-Apoe^-/- mice could be explained by the data on a Treg-DC coculture experiment showing the impaired ability of CCR4-deficient Tregs to downregulate CD80 and CD86 expression on DCs. As the reviewer pointed out, our data may indicate more permissive activation state of DCs and subsequent augmentation of effector T cell responses in Ccr4^-/-Apoe^-/- mice, which may be derived from impaired Treg suppressive function.

Assays for chemokine levels and influence on T cell activation and traffic:

Issue (1) Considering the findings described by Döring et al. (reference 24 in the paper), monitoring CCL22, CCL17, and CCL3 levels in the aorta and lymph nodes along atherosclerosis development would help in understanding when and how CCL17/CCL20-CCR4 might influence T cell activation and traffic. I wonder whether these chemokines were assayed by qPCR in lymphoid nodes and aorta from CCR4-deficient and sufficient Apoe^-/- mice. The authors report that CCR8 (capable also of binding CCL17) was unaltered by CCR4 deficiency in splenic and para-aortic lymph nodes Treg from 8 and 18 weeks-old mice, respectively (Supplementary Figure 5 and 6), although a trend towards a high-level was observed for splenic Treg. It would be informative to evaluate CCR8 Treg levels along with atherosclerosis progress.

As it is considered that the mRNA expression levels of chemokines do not necessarily reflect their protein expression levels, we did not analyze the mRNA expression of Ccl17 or Ccl22 by quantitative reverse transcription PCR. Instead of this, we evaluated the protein expression of CCL17 and CCL22 not only in the aorta but also in the peripheral lymph nodes of 18-week-old wild-type, Apoe^-/-, and Ccr4^-/-Apoe^-/- mice by immunohistochemistry. We found no marked differences in their expression levels in peripheral lymph nodes among these mice and included the data in Supplementary Figure 2.

As we focused on the role of the CCL17/CCL22–CCR4 axes in atherosclerosis, we did not examine the expression of CCL3 that is not directly related to these axes. The evaluation of CCR8+ Treg proportion is beyond the scope of this study, though we are interested in the change of this population by CCR4 deficiency associated with atherosclerotic lesion development.

Issue (2) According to IFNγ and IL-17 expressing TCD4⁺ subclasses, Th1 and Th17 cell subset levels increase in the spleen (Figure 3B-D) and para-aortic lymphoid nodes (Figure 4E) in CCR4 absence. A comparison of the CCR4 dependence for the migration of Th17 and Th1 cell subsets to the aorta was not performed in this atherosclerosis model; this study could help to understand the mechanisms associated with the aortic inflammation development.

To evaluate the migration of Th1 or Th17 cells in the aorta, we need to specifically isolate them from the peripheral lymphoid tissues of Apoe^-/- or Ccr4^-/-Apoe^-/- mice and adoptively transfer them into recipient Apoe^-/- mice. However, it is impossible to isolate alive Th1 or Th17 cells because specific cell surface markers that enable us to separate these cells are unavailable.

Issue (3) The numbers of Kaede Treg cells detected in the aorta were extremely low in both Apoe^-/- and Ccr4^-/-Apoe^-/- mice (Figure 5I), opening results to question. Besides, the flow cytometry assay used for determining Kaede Treg cells in tissues was not well described. How were cell viability and formation of doublets examined to avoid artefacts? The gating strategy used to ensure a confident analysis of Kaede Tregs, particularly in the aorta, should be included as supplementary material.

The extremely low number of Kaede-expressing Tregs migrated in the aorta of Apoe^-/- and Ccr4^-/-Apoe^-/- mice may be derived from the small number of the transferred Tregs. As another explanation for this finding, Tregs may rarely migrate in the aorta under hypercholesterolemic conditions. We did not check the viability or doublets of Kaede-expressing Tregs because we thought that such experimental procedures would not considerably affect the results. We provided the gating strategy of flow cytometric analysis of Kaede-expressing Tregs in peripheral lymphoid tissues and aortas in Supplementary Figure 11.

Other comments:

Issue (1) As an alternative for statistical data analysis from independent experiments, two-way ANOVA with Tukey's post hoc (for data normally distributed) or the Mack Skillings exact test with Conover´s post hoc multiple comparison test (for a two-way layout in non-parametric conditions) could improve analysis.

We performed statistical analysis in Figure 5A according to the reviewer’s suggestion.

Issue (2) For future work, employing recombinant pseudo-receptor proteins capable of neutralizing chemokines (doi: 10.1016/j.jhep.2021.08.029) might help as an alternative to complete knockout mice.

We thank the reviewer for giving us the information on an interesting approach as an alternative to CCR4-deficient mice.

Author response:

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

eLife Assessment

This study uses state-of-the-art methods to label endogenous dopamine receptors in a subset of Drosophila mushroom body neuronal types. The authors report that DopR1 and Dop2R receptors, which have opposing effects in intracellular cAMP, are present in axons termini of Kenyon cells, as well as those of two classes of dopaminergic neurons that innervate the mushroom body indicative of autocrine modulation by dopaminergic neurons. Additional experiments showing opposing effects of starvation on DopR1 and DopR2 levels in mushroom body neurons are consistent with a role for dopamine receptor levels increasing the efficiency of learned food-odour associations in starved flies. Supported by solid data, this is a valuable contribution to the field.

We thank the editors for the assessment, but request to change “DopR2” to “Dop2R”. The dopamine receptors in Drosophila have confusing names, but what we characterized in this study are called Dop1R1 (according to the Flybase; aka DopR1, dDA1, Dumb) and Dop2R (ibid; aka Dd2R). DopR2 is the name of a different dopamine receptor.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

This is an important and interesting study that uses the split-GFP approach. Localization of receptors and correlating them to function is important in understanding the circuit basis of behavior.

Strengths:

The split-GFP approach allows visualization of subcellular enrichment of dopamine receptors in the plasma membrane of GAL4-expressing neurons allowing for a high level of specificity.

The authors resolve the presynaptic localization of DopR1 and Dop2R, in "giant" Drosophila neurons differentiated from cytokinesis-arrested neuroblasts in culture as it is not clear in the lobes and calyx.

Starvation-induced opposite responses of dopamine receptor expression in the PPL1 and PAM DANs provide key insights into models of appetitive learning.

Starvation-induced increase in D2R allows for increased negative feedback that the authors test in D2R knockout flies where appetitive memory is diminished.

This dual autoreceptor system is an attractive model for how amplitude and kinetics of dopamine release can be fine-tuned and controlled depending on the cellular function and this paper presents a good methodology to do it and a good system where the dynamics of dopamine release can be tested at the level of behavior.

Weaknesses:

LI measurements of Kenyon cells and lobes indicate that Dop2R was approximately twice as enriched in the lobe as the average density across the whole neuron, while the lobe enrichment of Dop1R1 was about 1.5 times the average, are these levels consistent during different times of the day and the state of the animal. How were these conditions controlled and how sensitive are receptor expression to the time of day of dissection, staining, etc.

To answer this question, we repeated the experiment in two replicates at different times of day and confirmed that the receptor localization was consistent (Figure 3 – figure supplement 1); LI measurements showed that Dop2R is enriched more in the lobe and less in the calyx compared to Dop1R1 (Figure 3D). The states of animals that could affect LI (e.g. feeding state and anesthesia for sorting, see methods) were kept constant. 

The authors assume without discussion as to why and how presynaptic enrichment of these receptors is similar in giant neurons and MB.

In the revision, we added a short summary to recapitulate that the giant neurons exhibit many characteristics of mature neurons (Lines #152-156): "Importantly, these giant neurons exhibit characteristics of mature neurons, including firing patterns (Wu et al., 1990; Yao & Wu, 2001; Zhao & Wu, 1997) and acetylcholine release (Yao et al., 2000), both of which are regulated by cAMP and CaMKII signaling (Yao et al., 2000; Yao & Wu, 2001; Zhao & Wu, 1997)." In addition, we found punctate Brp accumulations localized to the axon terminals of the giant neurons (former Figure 4D and 4E). Therefore, the giant neuron serves as an excellent model to study the presynaptic localization of dopamine receptors in isolated large cells.

Figures 1-3 show the expensive expression of receptors in alpha and beta lobes while Figure 5 focusses on PAM and localization in γ and β' projections of PAM leading to the conclusion that presynaptic dopamine neurons express these and have feedback regulation. Consistency between lobes or discussion of these differences is important to consider.

In the revised manuscript, we show data in the γ KCs (Figure 4C, Figure 5 - figure supplement 1) in addition to α/β KCs, and demonstrate the consistent synaptic localization of Dop1R1 and Dop2R as in α/β KCs (Figure 4B and 5A). 

Receptor expression in any learning-related MBONs is not discussed, and it would be intriguing as how receptors are organized in those cells. Given that these PAMs input to both KCs and MBONs these will have to work in some coordination.

The subcellular localization of dopamine receptors in MBONs indeed provides important insights into the site of dopaminergic signaling in these neurons (Takemura et al., 2017; Pavlowsky et al., 2018; Pribbenow et al., 2022). Therefore, we added new data for Dop1R1 and Dop2R in MBON-γ1pedc>αβ (Figure 6). Interestingly, these receptors are localized to in the dendritic projection in the γ1 compartment as well as presynaptic boutons (Figure 6). 

Although authors use the D2R enhancement post starvation to show that knocking down receptors eliminated appetitive memory, the knocking out is affecting multiple neurons within this circuit including PAMs and KCs. How does that account for the observed effect? Are those not important for appetitive learning? 

In the appetitive memory experiment (Figure 9C), we knocked down Dop2R only in the select neurons of the PPL1 cluster, and this manipulation does not directly affect Dop2R expression in PAMs and KCs.

Starvation-induced enhancement of Dop2R expression in the PPL1 neurons (Figure 8F) would attenuate their outputs and therefore disinhibit expression of appetitive memory in starved flies (Krashes et al., 2009). Consistently, Dop2R knock-down in PPL1 impaired appetitive memory in starved flies (Figure 9C). We revised the corresponding text to make this point clearer (Lines #224227).

The evidence for fine-tuning is completely based on receptor expression and one behavioral outcome which could result from many possibilities. It is not clear if this fine-tuning and presynaptic feedback regulation-based dopamine release is a clear possibility. Alternate hypotheses and outcomes could be considered in the model as it is not completely substantiated by data at least as presented.

The reviewer’s concern is valid, and the presynaptic dopamine tuning by autoreceptors may need more experimental support. We therefore additionally discussed another possibility (Lines #289-291): “Alternatively, these presynaptic receptors could potentially receive extrasynaptic dopamine released from other DANs. Therefore, the autoreceptor functions need to be experimentally clarified by manipulating the receptor expression in DANs.”

Reviewer #2 (Public Review):

Summary:

Hiramatsu et al. investigated how cognate neurotransmitter receptors with antagonizing downstream effects localize within neurons when co-expressed. They focus on mapping the localization of the dopaminergic Dop1R1 and Dop2R receptors, which correspond to the mammalian D1- and D2-like dopamine receptors, which have opposing effects on intracellular cAMP levels, in neurons of the Drosophila mushroom body (MB). To visualize specific receptors in single neuron types within the crowded MB neuropil, the authors use existing dopamine receptor alleles tagged with 7 copies of split GFP to target reconstitution of GFP tags only in the neurons of interest as a read-out of receptor localization. The authors show that both Dop1R1 and Dop2R, with differing degrees, are enriched in axonal compartments of both the Kenyon Cells cholinergic presynaptic inputs and in different dopamine neurons (DANs), which project axons to the MB. Co-localization studies of dopamine receptors with the presynaptic marker Brp suggest that Dop1R1 and, to a larger extent Dop2R, localize in the proximity of release sites. This localization pattern in DANs suggests that Dop1R1 and Dop2R work in dual-feedback regulation as autoreceptors. Finally, they provide evidence that the balance of Dop1R1 and Dop2R in the axons of two different DAN populations is differentially modulated by starvation and that this regulation plays a role in regulating appetitive behaviors.

Strengths:

The authors use reconstitution of GFP fluorescence of split GFP tags knocked into the endogenous locus at the C-terminus of the dopamine receptors as a readout of dopamine receptor localization. This elegant approach preserves the endogenous transcriptional and post-transcriptional regulation of the receptor, which is essential for studies of protein localization.

The study focuses on mapping the localization of dopamine receptors in neurons of the mushroom body. This is an excellent choice of system to address the question posed in this study, as the neurons are well-studied, and their connections are carefully reconstructed in the mushroom body connectome. Furthermore, the role of this circuit in different behaviors and associative memory permits the linking of patterns of receptor localization to circuit function and resulting behavior. Because of these features, the authors can provide evidence that two antagonizing dopamine receptors can act as autoreceptors within the axonal compartment of MB innervating DANs. The differential regulation of the balance of the two receptors under starvation in two distinct DAN innervations provides evidence of the role that regulation of this balance can play in circuit function and behavioral output.

Weaknesses:

The approach of using endogenously tagged alleles to study localization is a strength of this study, but the authors do not provide sufficient evidence that the insertion of 7 copies of split GFP to the C terminus of the dopamine receptors does not interfere with the endogenous localization pattern or function. Both sets of tagged alleles (1X Venus and 7X split GFP tagged) were previously reported (Kondo et al., 2020), but only the 1X Venus tagged alleles were further functionally validated in assays of olfactory appetitive memory. Despite the smaller size of the 7X split-GFP array tag knocked into the same location as the 1X venus tag, the reconstitution of 7 copies of GFP at the C terminus of the dopamine receptor, might substantially increase the molecular bulk at this site, potentially impeding the function of the receptor more significantly than the smaller, single Venus tag. The data presented by Kondo et al. 2020, is insufficient to conclude that the two alleles are equivalent.

In the revision, we validated the function of these engineered receptors by a new set of olfactory learning experiments. Both these receptors in KCs were shown to be required for aversive memory (Kim et al., 2007, Scholz-Kornehl et al., 2016). As in the anatomical experiments, we induced GFP110 expression in KC of the flies homozygous for 7xGFP₁₁-tagged receptors using MB-Switch and 3 days of RU486 feeding o. We confirmed STM performance of these flies were not significantly different from the control (Figure 2 – figure supplement 1). Thus, these fusion receptors are functional.

The authors' conclusion that the receptors localize to presynaptic sites is weak. The analysis of the colocalization of the active zone marker Brp whole-brain staining with dopamine receptors labeled in specific neurons is insufficient to conclude that the receptors are localized at presynaptic sites. Given the highly crowded neuropil environment, the data cannot differentiate between the receptor localization postsynaptic to a dopamine release site or at a presynaptic site within the same neuron. The known distribution of presynaptic sites within the neurons analyzed in the study provides evidence that the receptors are enriched in axonal compartments, but co-labeling of presynaptic sites and receptors in the same neuron or super-resolution methods are needed to provide evidence of receptor localization at active zones.  The data presented in Figures 5K-5L provides compelling evidence that the receptors localize to neuronal varicosities in DANs where the receptors could play a role as autoreceptors.

Given the highly crowded environment of the mushroom body neuropil, the analysis of dopamine receptor localization in Kenyon cells is not conclusive. The data is sufficient to conclude that the receptors are preferentially localizing to the axonal compartment of Kenyon cells, but co-localization with brain-wide Brp active zone immunostaining is not sufficient to determine if the receptor localizes juxtaposed to dopaminergic release sites, in proximity of release sites in Kenyon cells, or both.

To better resolve the microcircuits of KCs, we triple-labeled the plasma membrane and DAR::rGFP in KCs, and Brp, and examined their localizations with high-resolution imaging with  Airyscan. This strategy revealed the receptor clusters associated with Brp accumulation within KCs (Figure 4). To further verify the association of DARs and active zones within KCs, we co-expressed Brp^short::mStraw and GFP_1-10 and confirmed their colocalization (Figure 5A), suggesting presynaptic localization of DARs in KCs. With these additional characterizations, we now discuss the significance of receptors at the presynaptic sites of KCs.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

This is an important and interesting study that uses the split-GFP approach. Localization of receptors and correlating them to function is important in understanding the circuit basis of behavior.

For Figure 1, the authors show PAM, PPL1 neurons, and the ellipsoid body as a validation of their tools (Dop1R1-T2A-GAL4 and Dop2R-T2A-GAL4) and the idea that these receptors are colocalized. However, it appears that the technique was applied to the whole brain so it would be great to see the whole brain to understand how much labelling is specific and how stochastic. Methods could include how dissection conditions were controlled and how sensitive are receptor expression to the time of day of dissection, staining, etc.

The expression patterns of the receptor T2A-GAL4 lines (Figure 1A and 1B) are consistent in the multiple whole brains (Kondo et al., 2020, Author response image 1).

Author response image 1.

The significance of the expression of these two receptors in an active zone is not clearly discussed and presynaptic localization is not elaborated on. Would something like expansion microscopy be useful in resolving this? It would be important to discuss that as giant neurons in culture don't replicate many aspects of the MB system.

In the revised manuscript, we elaborated discussion regarding the function of the two antagonizing receptors at the AZ (Lines #226-275).

Does MB-GeneSwitch > GFP1-1 reliably express in gamma lobes? Most of the figures show alpha/beta lobes.

Yes. MB-GeneSwitch is also expressed in γ KCs, but weakly. 12 hours of RU486 feeding, which we did in the previous experiments, was insufficient to induce GFP reconstitution in the γ KCs. By extending the time of transgene induction, we visualized expression of Dop1R1 and Dop2R more clearly in γ KCs. Their localization is similar to that in the α/β KCs (Figure 4C, Figure 5 - figure supplement 1).

Figure 6, y-axis says protein level. At first, I thought it was related to starvation so maybe authors can be more specific as the protein level doesn't indicate any aspect of starvation.

We appreciate this comment, and the labels on the y-axis were now changed to “rGFP levels” (Figure 8C and 8F, Figure 8 - figure supplement 1B, 1D and 1F).

Reviewer #2 (Recommendations For The Authors):

Title:

The title of the manuscript focuses on the tagging of the receptors and their synaptic enrichment.

Given that the alleles used in the study were generated in a previously published study (Kondo et al, 2020), which describes the receptor tagging and that the data currently provided is insufficient to conclude that the receptors are localizing to synapses, the title should be changed to reflect the focus on localizing antagonistic cognate neurotransmitter receptors in the same neuron and their putative role as autoreceptors in DANs.

Following this advice, we removed the methodology from the title and revised it to “Synaptic enrichment and dynamic regulation of the two opposing dopamine receptors within the same neurons”.

Minor issues with text and figures:

Figure 1

A conclusion from Figure 1 is that the two receptors are co-expressed in Kenyon cells. Please provide panels equivalent to the ones shown in D-G, with Kenyon cells cell bodies, or mark these cells in the existing panels, if present. Line 111 refers to panel 1D as the Kenyon cells panel, which is currently a PAM panel.

We added images for coexpression of these receptors in the cell bodies of KCs (Figure 1 - figure supplement 1) and revised the text accordingly (Lines #89-90).

Given that most of the study centers on visualizing receptor localization, it would benefit the reader to include labels in Figure 1 that help understand that these panels reflect expression patterns rather than receptor localization. For instance, rCD2::GFP could be indicated in the Dop1R1-LexA panels.

As suggested, labels were added to indicate the UAS and lexAop markers (Figure 1D, 1E, 1G-1I and Figure 1 – figure supplement 1).

Given that panels D-E focus on the cell bodies of the neurons, it could be beneficial for the reader to present the ellipsoid body neurons using a similar view that only shows the cell bodies. Similarly, one could just show the glial cell bodies .

We now show the cell bodies of ring neurons (Figure 1G) and ensheathing glia (Figure 1I).

For panel 1E, please indicate the subset of PPL1 neurons that both expressed Dop1R1 and Dop2R, as indicated in the text, as it is currently unclear from the image.

Dop1R1-T2A-LexA was barely detected in all PPL1 (Figure 1E). We corrected the confusing text (Lines #95-96).

Figure 2

The cartoon of the cell-type-specific labeling should show that the tag is 7XFP-11 and the UAScomponent FP-10, as the current cartoon leads the reader to conclude that the receptors are tagged with a single copy of split GFP. The detail that the receptors are tagged with 7 copies of split GFP is only provided through the genotype of the allele in the resource table.  This design aspect should be made clear in the figure and the text when describing the allele and approach used to tag receptors in specific neuron types.

We now added the construct design in the scheme (Figure 2A) and revised the corresponding text (Line #101-103).

Panel A. The arrow representing the endogenous promoter in the yellow gene representation should be placed at the beginning of the coding sequence. Currently, the different colors of what I assume are coding (yellow) and non-coding (white) transcript regions are not described in the legend.  I would omit these or represent them in the same color as thinner boxes if the authors want to emphasize that the tag is inserted at the C terminus within the endogenous locus.

The color scheme was revised to be more consistent and intuitive (Figure 2A).

Figure 3

Labels of the calyx and MB lobes would benefit readers not as familiar with the system used in the study. In addition, it would be beneficial to the reader to indicate in panel A the location of the compartments analyzed in panel H (e.g., peduncle, α3).

Figure 3A was amended to clearly indicate the analyzed MB compartments.

Adding frontal and sagittal to panels B-E, as in Figure 2, would help the reader interpret the data. 

In Figure 3B, “Frontal” and “Sagittal” were indicated.

Panel F-G. A scale bar should be provided for the data shown in the insets. Could the author comment on the localization of Dop1R1 in KCs? The data in the current panel suggests that only a subset of KCs express high levels of receptors in their axons, as a portion of the membrane is devoid of receptor signals. This would be in line with differential dopamine receptor expression in subsets of Kenyon cells, as shown in Kondo et al., 2020, which is currently not commented on in the paper. 

We confirmed that the majority of the KCs express both Dop1R1 and Dop2R genes (Figure 1 - figure supplement 1). LIs should be compared within the same cells rather than the differences of protein levels between cell types as they also reflect the GAL4 expression levels. 

Panel H. Some P values are shown as n.s. (p> 0.05). Other non-significant p values in this panel and in other figures throughout the paper are instead reported (e.g. peduncle P=0.164). For consistency, please report the values as n.s. as indicated in the methods for all non-significant tests in this panel and throughout the manuscript.

We now present the new dataset, and the graph represents the appropriate statistical results (Figure 3D; see the methods section for details).

The methods of labeling the receptors through the expression of the GeneSwitch-controlled GFP1-10 in Kenyon cells induced by RU486 are not provided in the methods. Please provide a description of this as referenced in the figure legend and the genotypes used in the analysis shown in the panels.

The method of RU486 feeding has been added. We apologize for the missing method.

Figure 4

Please provide scale bars for the inset in panels A-B.

Scale bars were added to all confocal images.

The current analysis cannot distinguish between postsynaptic and presynaptic dopamine receptors in KCs, and the figure title should reflect this.

We now present the new data dopamine receptors in KCs and clearly distinguish Brp clusters of the KCs and other cell types (Figure 4, Figure 5).

The reader could benefit from additional details of using the giant neuron model, as it is not commonly used, and it is not clear how to relate this to interpret the localization of dopaminergic receptors within Kenyon cells. The use of the venus-tagged receptor variant should be introduced in the text, as using a different allele currently lacks context. Figures 4F-4J show that the receptor is localizing throughout the neuron. Quantifying the fraction of receptor signal colocalizing with Brp could aid in interpreting the data.  However, it would still not be clear how to interpret this data in the context of understanding the localization of the receptors in neurons within fly brain circuits. In the absence of additional data, the data provided in Figure 4 is inconclusive and could be omitted, keeping the focus of the study on the analysis of the two receptors in DANs. Co-expressing a presynaptic marker in Kenyon cells (e.g., by expressing Brp::SNAP)  in conjunction with rGFP labeled receptor would provide additional evidence of the relationship of release sites in Kenyon cells and tagged dopamine receptors in these same cells and could add evidence in support to the current conclusion.

Following the advice, we added a short summary to recapitulate that the giant neurons exhibit many characteristics of mature neurons (Lines #152-156): "Importantly, these giant neurons exhibit characteristics of mature neurons, including firing patterns (Wu et al., 1990; Yao & Wu, 2001; Zhao & Wu, 1997) and acetylcholine release (Yao et al., 2000), both of which are regulated by cAMP and CaMKII signaling (Yao et al., 2000; Yao & Wu, 2001; Zhao & Wu, 1997)." Therefore, the giant neuron serves as an excellent model to study the presynaptic localization in large cells in isolation.

To clarify polarized localization of Brp clusters and dopamine receptors but not "localizing throughout the neuron", we now show less magnified data (Figure 5C). It clearly demonstrates punctate Brp accumulations localized to the axon terminals of the giant neurons (former Figure 4D and 4E). This is the same membrane segment where Dop1R1 and Dop2R are localized (Figure 5C). Therefore, the association of Brp clusters and the dopamine receptors in the isolated giant neurons suggests that the subcellular localization in the brain neurons is independent of the circuit context. 

As the giant neurons do not form intermingled circuits, venus-tagged receptors are sufficient for this experiment and simpler in genetics.

Following the suggestion to clarify the AZ association of the receptors in KCs, we coexpressed Brpshort-mStraw and GFP1-10 in KCs and confirmed their colocalization (Figure 5A).

Figure 6

The data and analysis show that starvation induces changes in the α3 compartment in PPL1 neurons only, while the data provided shows no significant change for PPL1 neurons innervating other MB compartments. This should be clearly stated in lines 174-175, as it is implied that there is a difference in the analysis for compartments other than α3. Panel L of Figure 6 - supplement 1 shows no significant change for all three compartments analyzed and should be indicated as n.s. in all instances, as stated in the methods. 

We revised the text to clarify that the starvation-induced differences of Dop2R expression were not significant (Lines #217-219). The reason to highlight the α3 compartment is that both Dop1R1 and Dop2R are coexpressed in this PPL1 neuron (Figure 8D).

Additional minor comments:

There are a few typos and errors throughout the manuscript. The text should be carefully proofread to correct these. Here are the ones that came to my attention:

Please reference all figure panels in the text. For instance, Figure 3A is not mentioned and should be revised in line 112 as Figure 3A-E.

Lines 103-104. The sentence "LI was visualized as the color of the membrane signals" is unclear and should be revised. 

Figure 4 legend - dendritic claws should likely be B and C and not B and E.

Lines 147 - Incorrect figure panels, should be 5C-L or 5D-E.

Line 241 - DNAs should be DANs.

Methods - please define what the abbreviation CS stands for.

We really appreciate for careful reading of this reviewer. All these were corrected.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

Shen et al. conducted three experiments to study the cortical tracking of the natural rhythms involved in biological motion (BM), and whether these involve audiovisual integration (AVI). They presented participants with visual (dot) motion and/or the sound of a walking person. They found that EEG activity tracks the step rhythm, as well as the gait (2-step cycle) rhythm. The gait rhythm specifically is tracked superadditively (power for A+V condition is higher than the sum of the A-only and V-only condition,

Experiments 1a/b), which is independent of the specific step frequency (Experiment 1b). Furthermore, audiovisual integration during tracking of gait was specific to BM, as it was absent (that is, the audiovisual congruency effect) when the walking dot motion was vertically inverted (Experiment 2). Finally, the study shows that an individual's autistic traits are negatively correlated with the BM-AVI congruency effect.

Strengths:

The three experiments are well designed and the various conditions are well controlled. The rationale of the study is clear, and the manuscript is pleasant to read. The analysis choices are easy to follow, and mostly appropriate.

Weaknesses:

On revision, the authors are careful not to overinterpret an analysis where the statistical test is not independent from the data (channel) selection criterion.

Thanks for the suggestion and we have done this according to your recommendations below.

Reviewer #1 (Recommendations for the authors):

Re: the double-dipping concern: I appreciate the revision. Just to clarify: my concern rests with the selection of *electrodes* based on the interaction test for the 1Hz condition. The 2Hz condition analogous test yields no significant electrodes. You perform subsequent tests (t-tests and 3-way interaction) on the data averaged across the electrodes that were significant for the 1Hz condition. Therefore, these tests will be biased to find a pattern reflecting an interaction at 1Hz, while no similar bias exists for an effect at 2Hz. Therefore, there is a bias to observe a 3-way interaction, and simple effects compatible with a 2-way interaction only for 1Hz, not for 2Hz (which is exactly what you found). There is no good statistical alternative here, I appreciate that, but the bias exists nonetheless. I think the wording is improved in this revision, and the evidence is convincing even in light of this bias.

We are grateful for your thoughtful comments on the analytical methods. We appreciate your concerns regarding the potential bias of examining 3-way interaction based on electrodes yielding a 2-way interaction effect. To address this issue, we have conducted a bias-free analysis based on electrodes across the whole brain. The results showed a similar pattern of 3-way interaction as previously reported (p = 0.051), suggesting that the previous findings might not be caused by electrode selection. Given that the main results of Experiment 2 were not based on whole-brain analysis, we did not involve this analysis in the main text, and we have removed the three-way interaction results based on selected electrodes from the manuscript to reduce potential concerns. It is also noteworthy that, when performing analyses based on channels independent of the interaction effect at 1 Hz (i.e., significant congruency effects in the upright and inverted conditions, respectively, at 2Hz), we got similar results as reported in the main text (i.e., non-significant interaction and correlation at 2 Hz). These results were presented in the supplementary file in previous versions and mentioned in the correlation part of the Results section (see Fig. S2). Once again, we sincerely appreciate your careful review of our research. We hope the abovementioned points adequately address your concern.

Reviewer #2 (Public review):

Summary:

The authors evaluate spectral changes in electroencephalography (EEG) data as a function of the congruency of audio and visual information associated with biological motion (BM) or non-biological motion. The results show supra-additive power gains in the neural response to gait dynamics, with trials in which audio and visual information was presented simultaneously producing higher average amplitude than the combined average power for auditory and visual conditions alone. Further analyses suggest that such supra-additivity is specific to BM and emerges from temporoparietal areas. The authors also find that the BM-specific supra-additivity is negatively correlated with autism traits.

Strengths:

The manuscript is well-written, with a concise and clear writing style. The visual presentation is largely clear. The study involves multiple experiments with different participant groups. Each experiment involves specific considered changes to the experimental paradigm that both replicate the previous experiment's finding yet extend it in a relevant manner.

In the first revisions of the paper, the manuscript better relays the results and anticipates analyses, and this version adequately resolves some concerns I had about analysis details. In a further revision, it is clarified better how the results relate to the various competing hypotheses on how biological motion is processed.

Weaknesses:

Still, it is my view that the findings of the study are basic neural correlate results that offer only minimal constraint towards the question of how the brain realizes the integration of multisensory information in the service of biological motion perception, and the data do not address the causal relevance of observed neural effects towards behavior and cognition. The presence of an inversion effect suggests that the supraadditivity is related to cognition, but that leaves open whether any detected neural pattern is actually consequential for multi-sensory integration (i.e., correlation is not causation). In other words, the fact that frequency-specific neural responses to the [audio & visual] condition are stronger than those to [audio] and [visual] combined does not mean this has implications for behavioral performance. While the correlation to autism traits could suggest some relation to behavior and is interesting in its own right, this correlation is a highly indirect way of assessing behavioral relevance. It would be helpful to test the relevance of supra-additive cortical tracking on a behavioral task directly related to the processing of biological motion to justify the claim that inputs are being integrated in the service of behavior. Under either framework, cortical tracking or entrainment, the causal relevance of neural findings toward cognition is lacking.

Overall, I believe this study finds neural correlates of biological motion that offer some constraint toward mechanism, and it is possible that the effects are behaviorally relevant, but based on the current task and associated analyses this has not been shown (or could not have been, given the paradigm).

Reviewer #2 (Recommendations for the authors):

Thank you for your revisions; I have updated the Strengths section, and reworded the weaknesses section. I now concede that the neural effects observed offer some constraint towards what the neural mechanisms for AV integration for BM are, whereas in my previous review, I said too strongly that these results do not offer any information about mechanism.

Thank you again for your insightful thoughts and comments on our research. They have contributed greatly to enhancing the discussion of the article and provided valuable inspiration for future exploration of causal mechanisms.

Author response:

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

Reviewer #1 (Public Review):

Summary:

This paper investigates the mechanism of axon growth directed by the conserved guidance cue UNC-6/Netrin. Experiments were designed to distinguish between alternative models in which UNC-6/Netrin functions as either a short-range (haptotactic) cue or a diffusible (chemotactic) signal that steers axons to their final destinations. In each case, axonal growth cones execute ventrally directed outgrowth toward a proximal source of UNC-6/Netrin. This work concludes that UNC-6/Netrin functions as both a haptotactic and chemotactic cue to polarize the UNC-40/DCC receptor on the growth cone membrane facing the direction of growth. Ventrally directed axons initially contact a minor longitudinal nerve tract (vSLNC) at which UNC-6/Netrin appears to be concentrated before proceeding in the direction of the ventral nerve cord (VNC) from which UNC-6/Netrin is secreted. Time-lapse imaging revealed that growth cones appear to pause at the vSLNC before actively extending ventrally directed filopodia that eventually contact the VNC. Growth cone contacts with the vSLNC were unstable in unc-6 mutants but were restored by the expression of a membrane-tethered UNC-6 in vSLNC neurons. In addition, the expression of membrane-tethered UNC-6/Netrin in the VNC was not sufficient to rescue initial ventral outgrowth in an unc-6 mutant. Finally, dual expression of membrane-tethered UNC-6/Netrin in both vSLNC and VNC partially rescued the unc-6 mutant axon guidance defect, thus suggesting that diffusible UNC-6 is also required. This work is important because it potentially resolves the controversial question of how UNC-6/Netrin directs axon guidance by proposing a model in which both of the competing mechanisms, e.g., haptotaxis vs chemotaxis, are successively employed. The impact of this work is bolstered by its use of powerful imaging and genetic methods to test models of UNC-6/Netrin function in vivo thereby obviating potential artifacts arising from in vitro analysis.

Strengths:

A strength of this approach is the adoption of the model organism C. elegans to exploit its ready accessibility to live cell imaging and powerful methods for genetic analysis.

Weaknesses:

A membrane-tethered version of UNC-6/Netrin was constructed to test its haptotactic role, but its neuron-specific expression and membrane localization are not directly determined although this should be technically feasible. Time-lapse imaging is a key strength of multiple experiments but only one movie is provided for readers to review.

Thank you for your comments. We have now used SNAP labeling to directly visualize the localization of membrane tethered UNC-6 and confirmed UNC-6 is only detectable on the sublateral and ventral nerve cords (Figure S3A). These data have been added to the manuscript on page 15, lines 342-347. We have also provided a representative movie for each imaged genotype (Videos S2-10).

Reviewer #2 (Public Review):

Nichols et al studied the role of axon guidance molecules and their receptors and how these work as long-range and/or local cues, using in-vivo time-lapse imaging in C. elegans. They found that the Netrin axon guidance system works in different modes when acting as a long-range (chemotaxis) cue vs local cue (haptotaxis). As an initial context, they take advantage of the postembryonic-born neuron, PDE, to understand how its axon grows and then is guided into its target. They found that this process occurs in various discrete steps, during which the growth cone migrates and pauses at specific structures, such as the vSLNC. The role of the UNC-6/Netrin and UNC-40/DCC axon guidance ligand-receptor pair was then looked at in terms of its requirement for

(1) initial axon outgrowth direction

(2) stabilization at the intermediate target

(3) directional branching from the sublateral region or

(4) ventral growth from the intermediate target to the VNC.

They found that each step is disrupted in the unc-6/Netrin and unc-40/DCC mutants and observed how the localization of these proteins changed during the process of axon guidance in wild-type and mutant contexts. These observations were further supported by analysis of a mutant important for the regulation of Netrin signaling, the E3 ubiquitin ligase madd-2/Trim9/Trim67. Remarkably, the authors identified that this mutant affected axonal adhesion and stabilization, but not directional growth. Using membrane-tethered UNC-6 to specific localities, they then found this to be a consequence of the availability of UNC-6 at specific localities within the axon growth path. Altogether, this data and in-vivo analysis provide compelling evidence of the mechanistic foundation of Netrin-mediated axon guidance and how it works step by step.

The conclusions are well-supported, with both imaging and quantification of each step of axon guidance and localization of UNC-6 and UNC-40. Using a different type of neuron to validate their findings further supports their conclusions and strengthens their model. It's not yet known whether this model holds true for other ligand-receptor pairs, but the current work sets the stage for future analysis of other axon guidance molecules using time-lapse in-vivo imaging. There are still two outstanding questions that are important to address to support the authors' model and conclusions.

(1) The results of UNC-6-TM expression at different locations are clear and support the conclusions but need to consider that there's no diffusible UNC-6 available. What would happen if UNC-6 is tethered to the membrane in an otherwise completely 'normal' UNC-6 gradient. Does the axon guidance ensue normally or does it get stuck in the respective site of the membrane tethered-UNC-6 and doesn't continue to outgrow properly? This is an important control (expression of the UNC-6-TM at the vSLNC or VNC in the wild type background) that would help clarify this question and gain a better insight into the separability of both axon guidance steps and the ability to manipulate these.

Thank you for your comments. We expressed UNC-6<SUP>TM</SUP> at vSLNC and VNC in wild-type animals and examined adult morphology of both HSN and PDE in the control conditions you suggested. These data are available in Tables 1 and 2 with no statistical differences compared to wildtype animals. Second, we also provide still images of developing PDE axons near the vSLNC (Figure S3D) to confirm that this axon guidance step is intact when UNC-6<SUP>TM</SUP> is overexpressed in specific regions. Together, these data suggest that the TM rescue constructs do not interfere with endogenous axon guidance pathways. We have added these results to the manuscript on page 15, lines 347-349.

(2) Axon guidance systems do not work in a vacuum and are generally competing against each other. For example, the SLT-1/Slit and SAX-3/ROBO axon guidance ligand-receptor pair is also required for PDE, and other post-embryonic neurons, axon guidance. It would be interesting to test mutants for these genes with the membrane tethered-UNC-6 to determine if the different steps of axon guidance are disrupted and if so, to what degree these are disrupted.

Thank you for this suggestion. We have performed time-lapse imaging on slt-1 mutants and unc-6; slt-1 double mutants. These data are available in a new figure, Figure 3. Indeed, we found that slt-1 mutants showed abnormal direction of axon emergence and stabilization at the VNC but normal stabilization at vsLNC and axonal branching (Fig.3). These data can be found in the manuscript from pages 11-12, lines 248-269.

Reviewer #3 (Public Review):

Summary:

This manuscript from Nichols, Lee, and Shen tackles an important question of how unc6/netrin promotes axon guidance: i.e. haptotaxis vs chemotaxis. This has recently been a large topic of investigation and discussion in the axon guidance field. Using live cell imaging of unc6/netrin and unc40/DCC in several neurons that extend axons ventrally during development, as well as TM localized mutants of Unc6, they suggest that unc6 promotes first haptotaxis of the emerging growth cone followed by chemotaxis of the growth cone. This is timely, as a recent preprint from the Lundquist group, using a similar strategy to make only a TM anchored unc6 similarly found that this could rescue only the haptotaxis-like growth of the PDE neuron, but not the second phase of growth. However, their conclusions were quite different based on the overexpression of unc6 everywhere rescuing the second phase, and thus they conclude that a gradient is not present.

Strengths:

As this has been quite a controversy in both the invertebrate and vertebrate field, one strength of this paper is that they use an unc6-neon green to demonstrate unc6 localization, and show a gradient of localization.

Weaknesses:

This is important, although it could be strengthened by first showing a more zoomed-out image of unc6 in the animal, and second demonstrating the localization of the transmembrane anchored unc6 mutants, to help define what may be the "diffusible Unc6".

Thank you for your comments. We have performed both of these experiments. In Figure 6A, we provide a zoomed out image of PDE growth cone interacting with UNC-6::mNG prior to reaching the vSLNC. Notably, we do not observe an obvious gradient that extends into this more dorsal region of the animal. We have also shown the membrane localization of UNC-6^TM through SNAP labeling in Figure S3A. These data have been added to the manuscript on page 15, lines 342-347.

I suggest two additional experimental or analysis suggestions: First, the authors clarify the phenotype of ventral emergence of the growth cone. Though the manuscript images suggest that no matter the mutant there is ventral emergence of the growth cone, but then later defects, yet they claim ventral emergence defects with the UNC6 tethered mutants, but there is no comparison of rose plots. This is confusing and needs to be addressed.

Thank you for your comment. We have now included images (i.e. slt-1(eh15) and unc-6(ev400); slt-1(eh15) genotypes in Figure 3) and movies showing misoriented axon emergence. We have also provided an additional quantification that allows for statistical comparison of emergence angle across genotypes. This quantification takes the sine function of the angle to quantify the relative emergence trajectory across the dorsal-ventral axis. A value of 1 indicates 90° dorsal emergence, and -1 indicates 90° ventral emergence. Statistical comparisons across genotypes demonstrate that axons in both unc-6 and slt-1 mutants are misoriented relative to wild-type axons. These comparisons can be found in Figures S1B, 3C, S2B, S3C.

Second, I have concerns that the analysis of unc40 polarization may be misleading in some cases when there appears to indeed be accumulation in the growth cone, but since the only analysis shown is relative to the rest of the cell, that can be lost.

Thank you for sharing your concerns about the UNC-40 polarization quantifications. We have separately compared the value of the integrated density of UNC-40::GFP in each cellular domain (vSLNC-contacting area and the dorsal soma) between genotypes. While we did not include these comparisons in the original manuscript, we have now included them in the revised manuscript. Overall, these data support our conclusions that UNC-40 mispolarization occurs across the entire cell (Fig. S1F,G; S2E-H; S3E,F).

Author response:

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

Public Reviews:

Reviewer 1:

Comment 1: Within the scope of the current work there are no major weaknesses. That said, the authors themselves note pressing questions beyond the scope of this study that remain unanswered. For instance, the mechanistic nature of the interactions between FMO-4 and the other players in this story, for example in terms of direct protein-protein interactions, is not at all understood yet.

We thank the reviewer for the positive review, and fully agree and acknowledge that there are unanswered questions for future studies that are beyond the scope of this manuscript.

Reviewer 2:

Comment 1: The effects of carbachol and EDTA on intracellular calcium levels are inferred, especially in the tissues where fmo-4 is acting. Validating that these agents and fmo-4 itself have an impact on calcium in relevant subcellular compartments is important to support conclusions on how fmo-4 regulates and responds to calcium.

We thank the reviewer for this important suggestion. We agree that carbachol and EDTA can be broad agents and validating that they are altering calcium levels is very useful. While this is technically challenging, we attempted to address this by using neuronally expressed GCaMP7f calcium indicator worms and measuring their GFP fluorescence upon exposure to carbachol and EDTA. Assessing both short term and long term exposure to these agents, we were able to show that carbachol increases GFP fluorescence, indicating an increase in calcium levels, and EDTA decreases GFP fluorescence, indicating a decrease in calcium levels. Unfortunately, because FMO-4 is not neuronally expressed, we were not able to test the effects of FMO-4 on calcium in this strain, which would require hypodermal expression and possibly short-term modification of fmo-4 expression to test. We have made sure to temper our language about the indirect measures we used.

Comment 2: Experiments are generally reliant on RNAi. While in most cases experiments reveal positive results, indicating RNAi efficacy, key conclusions could be strengthened with the incorporation of mutants.

We appreciate and value this suggestion and agree that mutants could be helpful to strengthen our conclusions. We address this caveat in the discussion of the revised manuscript. We explain that we were concerned about knocking out key calcium regulating genes like itr-1 and mcu-1 that either already result in some level of sickness in the worms when knocked down (itr-1) or could lead to confounding metabolic changes if knocked out. We do find that our RNAi lifespan results are robust and reproducible, but we also understand and recognize the caveats that come with using RNAi knockdown instead of full deletion mutants.

Reviewer 3:

Comment 1: no obvious transcriptomic evidence supporting a link between fmo-4 and calcium signaling: either for knockout worms or fmo-4 overexpressing strains.

We thank the reviewer for this feedback. While there is some transcriptomic evidence, we agree that it is not overwhelming evidence. We do think that this evidence, combined with the phenotype observed under thapsigargin (i.e., significant reduction in worm size and significant delay or prevention of development), in addition to the genetic connections to calcium regulation, provide additional compelling evidence that FMO-4 interacts with calcium signaling.

Comment 2: no direct measures of alterations in calcium flux, signalling or binding that strongly support a connection with fmo-4.

As described in reviewer 2 comment 1, we have successfully used GCaMP7f worms to assess calcium flux upon exposure to carbachol and EDTA. This approach confirmed the changes in calcium expected from these compounds. Unfortunately, because FMO-4 is not neuronally expressed, we were not able to test the effects of FMO-4 on calcium in this strain, which would require hypodermal expression and possibly short-term modification of fmo-4 expression to test. We have made sure to temper our language about the indirect measures we used.

Comment 3: no measures of mitochondrial morphology or activity that strongly support a connection with fmo-4.

This is a great point, and something we are currently working on to include for a future manuscript. 

Comment 4: lack of a complete model that places fmo-4 function downstream of DR and mTOR signalling (first Results section), fmo-2 (second Results section) and at the same time explains connection with calcium signalling.

We thank the reviewer for this helpful feedback. We have included a more complete working model in our revision.

Recommendations for the authors:

Reviewer 1:

Comment 1: "We utilized fmo-4 (ok294) knockout (KO) animals on five conditions reported to extend lifespan in C. elegans." Here I believe "fmo-4 (ok294)" should be "fmo-4(ok294)". (No space).

We thank the reviewer for this helpful revision. We have made this change as suggested.

Comment 2: "Wild-type (WT) worms on DR experience a ~35% lifespan extension compared to fed WT worms, but when fmo-4 is knocked out this extension is reduced to ~10% and this interaction is significant by cox regression (p-value < 4.50e-6)." Here "cox regression" should be "Cox regression".

We have made this change as suggested.

Comment 3: "Having established this role, we continued lifespan analyses of fmo-4 KO worms exposed to RNAi knockdown of the S6-kinase gene rsks-1 (mTOR signaling), the von hippel lindau gene vhl-1 (hypoxic signaling), the insulin receptor daf-2 (insulin-like signaling), and the cytochrome c reductase gene cyc-1 (mitochondrial electron transport chain, cytochrome c reductase) (Fig 1C-F)." Here "von hippel lindau" should be "Von Hippel-Lindau".

We have made this change as suggested.

Comment 4: In three instances in the caption of Figure 5, the "4" in fmo-4 is not italicized when it should be.

We have made this change as suggested.

Comment 5: In two instances in the caption of Figure 7, the "4" in fmo-4 is not italicized when it should be, and in one instance in the caption of Figure 7, the "6" in atf-6 is not italicized when it should be.

We have made this change as suggested.

Comment 6: "Supplemental Data 3 provides the results of the Log-rank test and Cox regression analysis, which were run in Rstudio." Here Rstudio should be RStudio.

We have made this change as suggested.

Comment 7: In the references, within article titles italicization (e.g. of Caenorhabditis elegans) is frequently missing. While this is often an artifact introduced by reference management software, it should be corrected in the final manuscript.

We thank the reviewer for all the helpful revision suggestions. We have made sure all the references are properly italicized where necessary.

Reviewer 2:

Comment 1: While FMO-4 is clearly placed in the ER calcium pathway genetically, the molecular mechanism by which FMO-4 would alter ER calcium is unclear. Notably, Tuckowski et al. highlight this gap in the discussion as well.

We thank the reviewer for identifying this important caveat. We hope to address the molecular mechanism by which FMO-4 alters ER calcium in upcoming projects.

Comment 2: Determining whether overexpression of catalytically dead FMO-4 or introduction of an inactivating point mutant into the endogenous locus phenocopy FMO-4 OE and KO animals would help distinguish between mechanisms involving protein-protein interactions or downstream metabolic regulation.

We thank the reviewer for this valuable suggestion. This is an experiment we are hoping to do in the near future to better understand molecular mechanisms and protein-protein interactions.

Reviewer 3:

Comment 1: When measuring the effect of thapsigargin on development of fmo-4 mutants it would be great to use a developmental assay rather than quantifying normalized worm area. Also please add scale bars to Figure 3G and 4H, it seems that fmo-4 overexpression decreases worm size even in control conditions, clarify if this is the case.

We thank the reviewer for this feedback. In addition to quantifying normalized worm area in Figure 3G-I, we have added a developmental assay (Figure 3J) that shows the development time of wild-type worms on DMSO or thapsigargin as well as the fmo-4 OE worms on DMSO or thapsigargin. These data validate that the fmo-4 OE worm development is either delayed significantly or even prevented when the worms are treated with thapsigargin.

We have added scale bars to Figure 3G and 4H as suggested.

We also appreciate the reviewer’s observation of the fmo-4 overexpression worms appearing smaller than wild-type worms in control conditions. We looked through the replicates and found that just one replicate showed a significant decrease in worm size, as observed in our unrevised manuscript. We repeated this experiment twice more to gather more data and determined that the fmo-4 overexpression worms were ultimately not significantly different in size compared to wild-type worms. We have included the new images and quantifications in Figure 3G-I and Figure 4H-J in the revised manuscript.

Comment 2: correct or replace Supplementary Table 2, which is not showing a DAVID analysis as the title and text would suggest. We should see biological/molecular processes, effect sizes, p-values, ...

We thank the reviewer for identifying this issue. We have added more detail to the Supplementary Table 2 so that it is clearer what is being shown in each tab.

Comment 3: clarify the data presented in Supplementary Data 2 because it does not clearly explain what is shown

This is a great point, and we have added more detail to the Supplementary Data 2 to make sure the data are more clearly explained in each tab.

Comment 4: in Figure 5B the fluorescent images do not seem to reflect the quantification in panel 5C.

Thank you for this feedback. We re-analyzed our data to make sure the proper fluorescent images are included with their matching quantifications in Figure 5B-C.

Comment 5: where is Supplementary Data 3?

We thank the reviewer for noticing this. Supplementary Data 3 was accidentally missing from the first submission, and has now been added.

Comment 6: conceptually the last results section (regarding atf-6) does not add much to the story, I would consider removing these results

We appreciate this feedback. We have decided to keep Figure 7 because we think it helps to validate fmo-4’s role in calcium movement from the ER. While we show genetic interactions between fmo-4 and key genes involved in calcium regulation (crt-1, itr-1, and mcu-1), we think that showing how fmo-4 also interacts with atf-6, a known regulator of calcium homeostasis, strengthens and supports the genetic mechanisms of fmo-4 proposed in this manuscript.

Comment 7: the model proposed in Figure 7E is not convincingly supported by the results:<br /> o the arrows connecting atf-6, fmo-4 and crt-1 (calreticulin) suggest that fmo-4 is downstream of atf-6 and upstream of crt-1: Berkowitz 2020 showed that atf-6 knockdown downregulates calreticulin, so unless the authors show that this downregulation is mediated directly by fmo-4, the more likely explanation is that atf-6 knockdown affects calcium levels which in turn induces fmo-4 expression.

We thank the reviewer for this helpful feedback. We have addressed this by updating our proposed model. We used a solid arrow leading from the reduction of atf-6 to induction of fmo-4, as this is supported by our data in Figure 7A-B. We then used dashed arrows between fmo-4 and crt-1 as well as between atf-6 and crt-1 to indicate that more data is needed to clarify this part of the pathway.

Comment 8: Avoid pointing at a mitochondrial connection in the title as the only evidence supporting this interaction comes from the mcu-1 RNAi epistasis.

We appreciate the reviewer’s suggestion. We added another piece of evidence suggesting an interaction between fmo-4 and the mitochondria to Supplementary Figure 7G-H. Here we show that while fmo-4 OE worms are resistant to paraquat stress, knocking down vdac-1 (a calcium regulator located in the outer mitochondrial membrane), abrogates this effect. We have kept mitochondria in our title but have made sure to temper our language in the main text to avoid pointing to a strong mitochondrial connection, since we have two pieces of evidence connecting fmo-4 to the mitochondria.

Author response:

Reviewer #1 (Public review):  

Hüppe and colleagues had already developed an apparatus and an analytical approach to capture swimming activity rhythms in krill. In a previous manuscript they explained the system, and here they employ it to show a circadian clock, supplemented by exogenous light, produces an activity pattern consistent with "twilight" diel vertical migration (DVM; a peak at sunset, a midnight sink, and a peak in the latter half of the night). 

They used light:dark (LD) followed by dark:dark (DD) photoperiods at two times of the year to confirm the circadian clock, coupled with DD experiments at four times of year to show rhythmicity occurs throughout the year along with DVM in the wild population. The individual activity data show variability in the rhythmic response, which is expected. However, their results showed rhythmicity was sustained in DD throughout the year, although the amplitude decayed quickly. The interpretation of a weak clock is reasonable, and they provide a convincing justification for the adaptive nature of such a clock in a species that has a wide distributional range and experiences various photic environments. These data also show that exogenous light increases the activity response and can explain the morning activity bouts, with the circadian clock explaining the evening and late-night bouts. This acknowledgement that vertical migration can be driven by multiple proximate mechanisms is important. 

The work is rigorously done, and the interpretations are sound. I see no major weaknesses in the manuscript. Because a considerable amount of processing is required to extract and interpret the rhythmic signals (see Methods and previous AMAZE paper), it is informative to have the individual activity plots of krill as a gut check on the group data. 

The manuscript will be useful to the field as it provides an elegant example of looking for biological rhythms in a marine planktonic organism and disentangling the exogenous response from the endogenous one. Furthermore, as high latitude environments change, understanding how important organisms like krill have the potential to respond will become increasingly important. This work provides a solid behavioral dataset to complement the earlier molecular data suggestive of a circadian clock in this species. 

We appreciate the positive evaluation of our work by Reviewer 1, acknowledging our approach to record locomotor activity in krill as well as the importance of the findings in assessing krill’s potential to respond to environmental change in their habitat.  

Reviewer #2 (Public review):  

Summary: 

This manuscript provides experimental evidence on circadian behavioural cycles in Antarctic krill. The krill were obtained directly from krill fishing vessels and the experiments were carried out on board using an advanced incubation device capable of recording activity levels over a number of days. A number of different experiments were carried out where krill were first exposed to simulated light:dark (L:D) regimes for some days followed by continuous darkness (DD). These were carried out on krill collected during late autumn and late summer. A further set of experiments was performed on krill across three different seasons (summer, autumn, winter), where incubations were all DD conditions. Activity was measured as the frequency by which an infrared beam close to the top of the incubation tube was broken over unit time. Results showed that patterns of increased and decreased activity that appeared synchronised to the LD cycle persisted during the DD period. This was interpreted as evidence of the operation of an internal (endogenous) clock. The amplitude of the behavioural cycles decreased with time in DD, which further suggests that this clock is relatively weak. The authors argued that the existence of a weak endogenous clock is an adaptation to life at high latitudes since allowing the clock to be modulated by external (exogenous) factors is an advantage when there is a high degree of seasonality. This hypothesis is further supported by seasonal DD experiments which showed that the periodicity of high and low activity levels differed between seasons. 

Strengths 

Although there has been a lot of field observations of various circadian type behaviour in Antarctic krill, relatively few experimental studies have been published considering this behaviour in terms of circadian patterns of activity. Krill are not a model organism and obtaining them and incubating them in suitable conditions are both difficult undertakings. Furthermore, there is a need to consider what their natural circadian rhythms are without the overinfluence of laboratory-induced artefacts. For this reason alone, the setup of the present study is ideal to consider this aspect of krill biology.

Furthermore, the equipment developed for measuring levels of activity is well-designed and likely to minimise artefacts. 

We would like to thank Reviewer 2 for their positive assessment of our approach to study the influence of the circadian clock on krill behavior. We are delighted, that Reviewer 2 found our mechanistic approach in understanding daily behavioral patterns of Antarctic krill using the AMAZE set-up convincing, and that the challenging circumstances of working with a polar, non-model species are acknowledged.

Weaknesses 

I have little criticism of the rationale for carrying out this work, nor of the experimental design. Nevertheless, the manuscript would benefit from a clearer explanation of the experimental design, particularly aimed at readers not familiar with research into circadian rhythms. Furthermore, I have a more fundamental question about the relationship between levels of activity and DVM on which I will expand below. Finally, it was unclear how the observational results made here related to the molecular aspects considered in the Discussion. 

(1) Explanation of experimental design - I acknowledge that the format of this particular journal insists that the Results are the first section that follows the Introduction. This nevertheless presents a problem for the reader since many of the concepts and terms that would generally be in the Methods are yet to be explained to the reader. Hence, right from the start of the Results section, the reader is thrown into the detail of what happened during the LD-DD experiments without being fully aware of why this type of experiment was carried out in the first place. Even after reading the Methods, further explanation would have been helpful. Circadian cycle type research of this sort often entrains organisms to certain light cycles and then takes the light away to see if the cycle continues in complete darkness, but this critical piece of knowledge does not come until much later (e.g. lines 369372) leaving the reader guessing until this point why the authors took the approach they did. I would suggest the following (1) that more effort is made in the Introduction to explain the exact LD/DD protocols adopted (2) that a schematic figure is placed early on in the manuscript where the protocol is explained including some logical flow charts of e.g. if behavioural cycle continues in DD then internal clock exists versus if cycle does not continue in DD, the exogenous cues dominate - followed by - major decrease in cyclic amplitude = weak clock versus minor decrease = strong clock and so on 

We would like to thank Reviewer 2 for pointing out that the experimental design and the rationale behind it are not becoming clear early in the manuscript, especially for people outside the field of chronobiology. We think that the suggestion to include a schematic figure early in the manuscript is excellent and we plan to implement this in a revised version of the manuscript.  

(2) Activity vs kinesis - in this study, we are shown data that (i) krill have a circadian cycle - incubation experiments; (ii) that krill swarms display DVM in this region - echosounder data (although see my later point). My question here is regarding the relationship between what is being measured by the incubation experiments and the in situ swarm behaviour observations. The incubation experiments are essentially measuring the propensity of krill to swim upwards since it logs the number of times an individual (or group) break a beam towards the top of the incubation tube. I argue that krill may be still highly active in the rest of the tube but just do not swim close to the surface, so this approach may not be a good measure of "activity". Otherwise, I suggest a more correct term of what is being measured is the level of "upward kinesis". As the authors themselves note, krill are negatively buoyant and must always be active to remain pelagic. What changes over the day-night cycle is whether they decide to expend that activity on swimming upwards, downwards or remaining at the same depth. Explaining the pattern as upward kinesis then also explains by swarms move upwards during the night. Just being more active at night may not necessarily result in them swimming upwards. 

We believe that there is a slight misunderstanding in the way that what we call “activity” is measured. The experimental columns are equipped with five detector modules, evenly distributed over the height of the column. In our analysis we count all beam breaks that are caused by upward movement, i.e. every time a detector module is triggered after a detector module at a lower position has been triggered, and not only when the top detector module is triggered. In this way, we record upward swimming movements throughout the column, and not only when the krill swims all the way to the top of the column. This still means that what we are measuring is swimming activity, caused by upward swimming. We use this measure, to deliberately separate increased swimming activity, from baseline activity (i.e. swimming which solely compensates for negative buoyancy) and inactivity (i.e. passive sinking). 

A higher activity is thus at first interpreted as an increase in swimming activity, which in the field may result in upwards directed swimming but also could mean a horizontal increase in activity, for example representing increased foraging and feeding activity. This would explain the daily activity pattern observed under LD cycles (Fig. 2), which shows a general increase in activity during the dark phase. This nighttime increase could be used for both upward directed migration during sunset as well as horizontal directed swimming for feeding and foraging throughout the night.

We will formulate the description of the activity metric more clearly in the revised version of the manuscript.

(3) Molecular relevance - Although I am interested in molecular clock aspects behind these circadian rhythms, it was not made clear how the results of the present study allow any further insight into this. In lines 282 to 284, the findings of the study by Biscontin et al (2017) are discussed with regard to how TIM protein is degraded by light via the clock photreceptor CRYTOCHROME 1. This element of the Discussion would be a lot more relevant if the results of the present study were considered in terms of whether they supported or refuted this or any other molecular clock model. As it stands, this paragraph is purely background knowledge and a candidate for deletion in the interest of shortening the Discussion.  

We agree that this part is not directly related to the data presented in the manuscript and will therefore omit this part in the revised version of the manuscript to keep the discussion concise and focused on the results. 

Other aspects 

(i) 'Bimodal swimming' was used in the Abstract and later in the text without the term being fully explained. I could interpret it to mean a number of things so some explanation is required before the term is introduced. 

We thank the Reviewer for pointing this out and will provide an explanation for the term “bimodal swimming” in a revised version of the manuscript. 

(ii) Midnight sinking - I was struck by Figure 2b with regards to the dip in activity after the initial ascent, as well as the rise in activity predawn. Cushing (1951) Biol Rev 26: 158-192 describes the different phases of a DVM common to a number of marine organisms observed in situ where there is a period of midnight sinking following the initial dusk ascent and a dawn rise prior to dawn descent. Tarling et al (2002) observe midnight sinking pattern in Calanus finmarchicus and consider whether it is a response to feeding satiation or predation avoidance (i.e. exogenous factors). Evidence from the present study indicates that midnight sinking (and potential dawn rise) behaviour could alternatively be under endogenous control to a greater or lesser degree. This is something that should certainly be mentioned in the Discussion, possibly in place of the molecular discussion element mentioned above - possibly adding to the paragraph Lines 303-319. 

We would like to thank the Reviewer for pointing this out and agree that it would be interesting to add the idea of an endogenous control of midnight sinking to the discussion. We plan to implement this in a revised version of the manuscript. 

(iii) Lines 200-207 - I struggled to follow this argument regarding Piccolin et al identifying a 12 h rhythm whereas the present study indicates a ~24 h rhythm. Is one contradicting the other - please make this clear. 

In our study we found that the circadian clock drives a bimodal pattern of swimming activity in krill, meaning it controls two bouts of activity in a 24 h cycle. Piccolin et al. (2020) identified a swimming activity pattern of ~12 h (i.e. two peaks in 24 h) at the group level, which is in line with our findings at the individual level. We will revisit the mentioned section for more clarity in a revised version.   

(iv) Although I agree that the hydroacoustic data should be included and is generally supportive of the results, I think that two further aspects should be made clear for context (a) whether there was any groundtruthing that the acoustic marks were indeed krill and not potentially some other group know to perform DVM such as myctophids (b) how representative were these patterns - I have a sense that they were heavily selected to show only ones with prominent DVM as opposed to other parts of the dataset where such a pattern was less clear - I am aware of a lot of krill research where DVM is not such a clear pattern and it is disingenuous to provide these patterns as the definitive way in which krill behaves. I ask this be made clear to the reader (note also that there is a suggestion of midnight sinking in Fig 5b on 28/2).  

To clarify the mentioned points concerning the hydroacoustic data:

a) As mentioned in the Methods section, only hydroacoustic data during active fishing was included in the analysis. E. superba occurs in large monospecific aggregations and the fishery is actively targeting E. superba and monitoring their catch and the proportion of non-target species continuously with cameras. Krill fishery bycatch rates are very low (0.1–0.3%, Krafft et al. 2018), and fishing operations would stop if non-target species were being caught in significant proportions at any time. Therefore, and supported by our own observations when we conducted the experiments, we argue that it is a valid assumption that the backscattering signal shown in Figure 5 is predominantly caused by E. superba. 

b) We are aware of the fact that DVM patterns of Antarctic krill are highly variable and that normal DVM patterns do not need to be the rule (e.g. see our cited study on the plasticity of krill DVM by Bahlburg et al. 2023). The visualized data were not selected for their DVM pattern but represent the period directly preceding the sampling for behavioral experiments in four different seasons (namely S1-S4), including the day of sampling. These periods were chosen to assess the DVM behavior of krill swarms in the field in the days before and during the sampling for behavioral experiments. 

We will include these aspects in the Methods section in a revised version of the manuscript in order to improve understanding.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The authors' research group had previously demonstrated the release of large multivesicular body-like structures by human colorectal cancer cells. This manuscript expands on their findings, revealing that this phenomenon is not exclusive to colorectal cancer cells but is also observed in various other cell types, including different cultured cell lines, as well as cells in the mouse kidney and liver. Furthermore, the authors argue that these large multivesicular body-like structures originate from intracellular amphisomes, which they term "amphiectosomes." These amphiectosomes release their intraluminal vesicles (ILVs) through a "torn-bag mechanism." Finally, the authors demonstrate that the ILVs of amphiectosomes are either LC3B positive or CD63 positive. This distinction implies that the ILVs either originate from amphisomes or multivesicular bodies, respectively.

Strengths:

The manuscript reports a potential origin of extracellular vesicle (EV) biogenesis. The reported observations are intriguing.

Weaknesses:

It is essential to note that the manuscript has issues with experimental designs and lacks consistency in the presented data. Here is a list of the major concerns:

(1) The authors culture the cells in the presence of fetal bovine serum (FBS) in the culture medium. Given that FBS contains a substantial amount of EVs, this raises a significant issue, as it becomes challenging to differentiate between EVs derived from FBS and those released by the cells. This concern extends to all transmission electron microscopy (TEM) images (Figure 1, 2P-S, S5, Figure 4 P-U) and the quantification of EV numbers in Figure 3. The authors need to use an FBS-free cell culture medium.

Although FBS indeed contains bovine EVs, however, the presence of very large multivesicular EVs (amphiectosomes) that our manuscript focuses on has never been observed and reported. For reported size distributions of EVs in FBS, please find a few relevant references below:

PMID: 29410778, PMID: 33532042, PMID: 30940830 and PMID: 37298194

All the above publications show that the number of lEVs > 350-500 nm is negligible in FBS. The average diameter of MV-lEVs (amphiectosomes) described in our manuscript is around 1.00-1.50 micrometer.

Reviewer #1: These papers evaluated the effectiveness of various methods to eliminate EVs from FBS, emphasizing the challenges associated with the presence of EVs in FBS. They also caution against using FBS in EV studies due to these issues. However, I did not find a clear indication regarding the size distributions of EVs in FBS in these papers.

Please provide accurate reference supporting the claim that 'lEVs > 350-500 nm are negligible in FBS.' The papers cited by the authors do not address this specific point.

In the revised manuscript, we addressed the point that due to sterile filtering of FBS, it cannot contain large >0.22 µm EVs

Our response to Reviewer #1 point 2. When we demonstrated the TEM of isolated EVs, we consistently used serum- free conditioned medium (Fig2 P-S, Fig2S5 J, O) as described previously (Németh et al 2021, PMID: 34665280).

Reviewer #1: This is an important point that is not mentioned in the original main text, figure legend or method. Please address.

We agree and we apologize for it. We added this information to the revised manuscript.

Our response to Reviewer #1 point 3. Our TEM images show cells captured in the process of budding and scission of large multivesicular EVs excluding the possibility that these structures could have originated from FBS.

Reviewer #1: These images may also depict the engulfment of EVs in FBS. Hence, it is crucial to utilize EV-free or EV-depleted FBS.

As we mentioned earlier, we added the information to the revised manuscript that sterile filtering of the FBS presumably removed particles >0.22 µm EVs

Our response to Reviewer #1 point 4. In addition, in our confocal analysis, we studied Palm-GFP positive, cell-line derived MV-lEVs. Importantly, in these experiments, FBS-derived EVs are non-fluorescent, therefore, the distinction between GFP positive MV-lEVs and FBS-derived EVs was evident.

Reviewer #1: I agree that these fluorescent-labeled assays conclusively indicate that the MV-lEVs are originating from the cells. However, the images of concerns are the non- fluorescent-labeled images in (Figure 1, 2P-S, S5, Figure 4 P-U and Figure 3). The MV-lEVs may derive from both the cells and FBS.

Please see above our response to points 1-3.

Our response to Reviewer #1 point 5. In addition, culturing cells in FBS-free medium (serum starvation) significantly affects autophagy. Given that in our study, we focused on autophagy related amphiectosome secretion, we intentionally chose to use FBS supplemented medium.

Reviewer #1 If this is a concern, the authors should use EV-depletive FBS.

As we discussed above, sterile filtration of FBS removes particles >0.22 µm. In addition, based on our preliminary experiments, EV-depleted serum may effect cell physiology. 

Our response to Reviewer #1 point 6. Even though the authors of this manuscript are not familiar with the technological details how FBS is processed before commercialization, it is reasonable to assume that the samples are subjected to sterile filtration (through a 0.22 micron filter) after which MV-lEVs cannot be present in the commercial FBS samples.

Reviewer #1This is a fair comment that needs to be included in the manuscript.

As you suggested, this comment is now included in the revised manuscript

(2) The data presented in Figure 2 is not convincingly supportive of the authors' conclusion. The authors argue that "...CD81 was present in the plasma membrane-derived limiting membrane (Figures 2B, D, F), while CD63 was only found inside the MV-lEVs (Fig. 2A, C, E)." However, in Figure 2G, there is an observable CD63 signal in the limiting membrane (overlapping with the green signals), and in Figure 2J, CD81 also exhibits overlap with MV-IEVs.

Both CD63 and CD81 are tetraspanins known to be present both in the membrane of sEVs and in the plasma membrane of cells (for references, please see Uniprot subcellular location maps: https://www.uniprot.org/uniprotkb/P08962/entry#subcellular_location https://www.uniprot.org/uniprotkb/P60033/entry#subcellular_location). However, according the feedback of the reviewer, for clarity, we will delete the implicated sentence from the text.

Reviewer #1 Please also justify the statement questioned in (3) as these arguments are interconnected.

We hope you find our above responses to your comment acceptable.

(3) Following up on the previous concern, the authors argue that CD81 and CD63 are exclusively located on the limiting membrane and MV-IEVs, respectively (Figure 2-A-M). However, in lines 104-106, the authors conclude that "The simultaneous presence of CD63, CD81, TSG101, ALIX, and the autophagosome marker LC3B within the MV-lEVs..." This statement indicates that CD63 and CD81 co-localize to the MV-IEVs. The authors need to address this apparent discrepancy and provide an explanation.

There must be a misunderstanding because we did not claim or implicate in the text that “CD81 and CD63 are exclusively located on the limiting membrane and MV-IEVs”. Here we studied co-localization of the above proteins in the case intraluminal vesicles (ILVs). In Fig 2. we did not show any analysis of limiting membrane co-localization.

Reviewer #1 I have indicated that this statement is found in lines 104-106, where the authors argue, 'The simultaneous presence of CD63, CD81, TSG101, ALIX, and the autophagosome marker LC3B within the MV-lEVs...' If the authors acknowledge the inaccuracy of this statement, please provide a justification for this argument.

For clarity, we modified the description of data shown in Fig2 in the revised manuscript.

(4) The specificity of the antibodies used in Figure 2 should be validated through knockout or knockdown experiments. Several of the antibodies used in this figure detect multiple bands on western blots, raising doubts about their specificity. Verification through additional experimental approaches is essential to ensure the reliability and accuracy of all the immunostaining data in this manuscript.

We will consider this suggestion during the revision of the manuscript.

Reviewer #1:Please do so.

We carefully considered the suggestion, but we realized that it was not feasible for us to perform gene silencing in the case of all our used antibodies before resubmission of our revised manuscript. However, we repeated the Western blot for mouse anti-CD81 (Invitrogen MAA5-13548) and replaced the previous Western blot by it in the revised manuscript (Fig.2-S4H)

(5) In Figures 2P-R, the morphology of the MV-IEVs does not resemble those shown in Figures 1-A, H, and D, indicating a notable inconsistency in the data.

EM images in Figure2 P-R show sEVs separated from serum-free conditioned media as opposed to MV-lEVs, which were in situ captured in fixed tissue cultures (Fig1). Therefore, the two EV populations necessarily have different size and structure. Furthermore, Fig. 1 shows images of ultrathin sections while in Figure 2P-R, we used a negative-positive contrasting of intact sEV-s without embedding and sectioning.

(6) There are no loading controls provided for any of the western blot data.

Not even the latest MISEV 2023 guidelines give recommendations for proper loading control for separated EVs in Western blot (MISEV 2023 , DOI: 10.1002/jev2.12404 PMID: 38326288). Here we applied our previously developed method (PMID: 37103858), which in our opinion, is the most reliable approach to be used for sEV Western blotting. For whole cell lysates, we used actin as loading control (Fig3-S2B).

Reviewer #1: The blots referenced here (Fig2-S3; Fig2-S4B; Fig3-S2B) were conducted using total cell lysates, not EV extracts. Only one blot in Fig3-S2B includes an actin control. All remaining blots should incorporate actin controls for consistency.

Fig2-S3 (corresponding to Fig2-S4 in the revised manuscript) only shows reactivity of the used antibodies. This Western blot is not intended to serve as a basis of any quantitative conclusions. Fig2-S4 (corresponding to Fig2-S5 in the revised manuscript) includes the actin control. Fig3-S2B shows the complete membrane, which was cut into 4 pieces, and the immune reactivity of different antibodies was tested. The actin band was included on the anti-LC3B blot. For clarity, we rephrased the figure legend.

Additionally, for Figures 2-S4B, the authors should run the samples from lanes i-iii in a single gel.

Please note that in Figure 2- S4B, we did run a single gel, and the blot was cut into 4 pieces, which were tested by anti-GFP, anti-RFP, anti-LC3A and anti-LC3B antibodies. Full Western blots are shown in Fig.3_S2 B, and lanes “1”, “2” and “3” correspond to “i”, “ii” and “iii” in Fig.2-S4, respectively.

Reviewer #1: In the original Figure 2- S4B, the blots were sectioned into 12 pieces. If lanes "i," "ii," and "iii" were run on the same blot, the authors are advised to eliminate the grids between these lanes.

Grids separating the lanes have been eliminated on Fig.2_S4 (now Fig.2_S5 in the revised manuscript).

(7) In Figure 2-S4, is there co-localization observed between LC3RFP (LC3A?) with other MV-IFV markers? How about LC3B? Does LC3B co-localize with other MV-IFV markers?

In Supplementary Figure 2-S4, we showed successful generation of HEK293T-PalmGFP-LC3RFP cell line. In this case we tested the cells, and not the released MV-lEVs. LC3A co-localized with the RFP signal as expected.

Reviewer #1: Does LC3RFP colocalize with MV-IFV markers in HEK293T-PalmGFP-LC3RFP cell line? This experiment aims to clarify the conclusion made in lines 104-106, where the authors assert that 'The concurrent existence of CD63, CD81, TSG101, ALIX, and the autophagosome marker LC3B within the MV-lEVs...'

In the case of PalmGFP-LC3RFP cells, LC3-RFP is overexpressed. Simultaneous assessment of this overexpressed protein with non-overexpressed, fluorescent antibod-detected molecules proved to be challenging because of spectral overlaps and inappropriate signal-noise ratios. Furthermore, in association with EVs, the number of antibody-detected molecules is substantially lower than in cells. Therefore, even though we tried, we could not successfully perform these experiments.

(8) The TEM images presented in Figure 2-S5, specifically F, G, H, and I, do not closely resemble the images in Figure 2-S5 K, L, M, N, and O. Despite this dissimilarity, the authors argue that these images depict the same structures. The authors should provide an explanation for this observed discrepancy to ensure clarity and consistency in the interpretation of the presented data.

As indicated in Material and Methods, Fig 2-S5 F, G, H and I are conventional TEM images fixed by 4% glutaraldehyde 1% OsO₄ 2h and embedded into Epon resin with a post contrasting of 3.75% uranyl acetate 10 min and 12 min lead citrate. Samples processed this way have very high structure preservation and better image quality, however, they are not suitable for immune detection. In contrast, Fig.2.-S5 K,L,M,N shows immunogold labelling of in situ fixed samples. In this case we used milder fixation (4% PFA, 0.1% glutaraldehyde, postfixed by 0.5% OsO₄ 30 min) and LR-White hydrophilic resin embedding. This special resin enables immunogold TEM analysis. The sections were exposed to H₂O₂ and NaBH₄ to render the epitopes accessible in the resin. Because of the different applied techniques, the preservation of the structure is not the same. In the case of Fig.2 J, O, separated sEVs were visualised by negative-positive contrast and immunogold labelling as described previously (PMID: 37103858).

Reviewer #1: Please include this justification in the revised version.

We included this justification in the revised manuscript.

(9) For Figures 3C and 3-S1, the authors should include the images used for EV quantification. Considering the concern regarding potential contamination introduced by FBS (concern 1), it is advisable for the authors to employ an independent method to identify EVs, thereby confirming the reliability of the data presented in these figures.

In our revised manuscript, we will provide all the images used for EV quantification in Figure 3C. Given that Figures 3C and 3-S1 show MV-lEVs released by HEK293T-PlamGFP cells, the possible interference by FBS-derived non-fluorescent EVs can be excluded.

Reviewer #1: Please provide all the images.

Original LASX files are provided (DOI: 10.6019/S-BIAD1456 ).

Reviewer #1: The images raising concerns regarding the contamination of EVs in FBS primarily consist of transmission electron microscopy (TEM) images, namely, Figure 1, 2P-S, S5, and Figure 4 P-U, along with the quantification of EV numbers in Figure 3. These concerns persist despite the use of fluorescent-labeled experiments. While fluorescent-labeled MV-lEVs are conclusively identified as originating from the cells, the MV-lEVs observed in Figure 1, 2P-S, S5, and Figure 4 P-U and Figure 3 may derive from both the cells and FBS.

Large EVs (with diameter >800 nm) derived from FBS were not present in our experiments, as discussed above.

(10) Do the amphiectosomes released from other cell types as well as cells in mouse kidneys or liver contain LC3B positive and CD63 positive ILVs?

Based on our confocal microscopic analysis, in addition the HEK293T-PalmGFP cells, HT29 and HepG2 cells also release similar LC3B and CD63 positive MV-lEVs. Preliminary evidence shows MV-lEV secretion by additional cell types.

The response of Reviewer #1: Please show these data in the revised manuscript. Moreover, do cells in mouse kidneys or liver contain LC3B positive and CD63 positive ILVs?

We have added new confocal microscopic images to Fig2-S3 showing amphiectosomes released also by the H9c2 (ATCC) cardiomyoblast cell line. To preserve the ultrastructure of MV-lEVs in complex organs like kidney and liver, fixation with 4% glutaraldehyde with 1% OsO4 appears to be essential. This fixation does not allow for immune detection to assess LC3B and CD63 positive MV-lEVs in the ultrathin sections.

Reviewer #2 (Public Review):

Summary:

The authors had previously identified that a colorectal cancer cell line generates small extracellular vesicles (sEVs) via a mechanism where a larger intracellular compartment containing these sEVs is secreted from the surface of the cell and then tears to release its contents. Previous studies have suggested that intraluminal vesicles (ILVs) inside endosomal multivesicular bodies and amphisomes can be secreted by the fusion of the compartment with the plasma membrane. The 'torn bag mechanism' considered in this manuscript is distinctly different because it involves initial budding off of a plasma membrane-enclosed compartment (called the amphiectosome in this manuscript, or MV-lEV). The authors successfully set out to investigate whether this mechanism is common to many cell types and to determine some of the subcellular processes involved.

The strengths of the study are:

(1) The high-quality imaging approaches used, seem to show good examples of the proposed mechanism.

(2) They screen several cell lines for these structures, also search for similar structures in vivo, and show the tearing process by real-time imaging.

(3) Regarding the intracellular mechanisms of ILV production, the authors also try to demonstrate the different stages of amphiectosome production and differently labelled ILVs using immuno-EM.

Several of these techniques are technically challenging to do well, and so these are critical strengths of the manuscript.

The weaknesses are:

(1) Most of the analysis is undertaken with cell lines. In fact, all of the analysis involving the assessment of specific proteins associated with amphiectosomes and ILVs are performed in vitro, so it is unclear whether these processes are really mirrored in vivo. The images shown in vivo only demonstrate putative amphiectosomes in the circulation, which is perhaps surprising if they normally have a short half-life and would need to pass through an endothelium to reach the vessel lumen unless they were secreted by the endothelial cells themselves.

Our previous results analyzing PFA-fixed, paraffin embedded sections of colorectal cancer patients provided direct evidence that MV-lEV secretion also occurs in humans in vivo (PMID: 31007874). Regarding your comment on the presence of amphiectosomes in the circulation despite their short half-lives, we would like to point out that Fig1.X shows a circulating lymphocyte which releases MV-lEV within the vessel lumen. Furthermore, in the revised manuscript, an additional Fig.1-S1 is provided. Here, we show the release of MV-lEVs both by an endothelial and a sub-endothelial cell (Fig.1-S1G). In addition, these images show the simultaneous presence of MV-lEVs and sEVs in the circulation (Fig.1-S1.A,C,D,H and I). The transmission electron micrographs of mouse kidney and liver sections provide additional evidence that the MV-lEVs are released by different types of cells, and the “torn bag release” also takes place in vivo (Fig.1.V).

(2) The analysis of the intracellular formation of compartments involved in the secretion process (Figure 2-S5) relies on immuno-EM, which is generally less convincing than high-/super-resolution fluorescence microscopy because the immuno-labelling is inevitably very sporadic and patchy. High-quality EM is challenging for many labs (and seems to be done very well here), but high-/super-resolution fluorescence microscopy techniques are more commonly employed, and the study already shows that these techniques should be applicable to studying the intracellular trafficking processes.

As you suggested, in the revised manuscript, we present additional super-resolution microscopy (STED) data. The intracellular formation of amphisomes, the fragmentation of LC3B-positive membranes and the formation of LC3B-positive ILVs were captured (Fig. 3B-F).

(3) One aspect of the mechanism, which needs some consideration, is what happens to the amphisome membrane, once it has budded off inside the amphiectosome. In the fluorescence images, it seems to be disrupted, but presumably, this must happen after separation from the cell to avoid the release of ILVs inside the cell. There is an additional part of Figure 1 (Figure 1Y onwards), which does not seem to be discussed in the text (and should be), that alludes to amphiectosomes often having a double membrane.

We agree with your comment regarding the amphisome membrane and we added a sentence to the Discussion of the revised manuscript. Fig1Y onwards is now discussed in the manuscript. In addition, we labelled the surface of living HEK293 cells with wheat germ agglutinin (WGA), which binds to sialic acid and N-acetyl-D-glucosamine. After removing the unbound WGA by washes, the cells were cultured for an additional 3 hours, and the release of amphiectosomes was studied. The budding amphiectosome had WGA positive membrane providing evidence that the external limiting membrane had a plasma membrane origin (Fig.3G)

(4) The real-time analysis of the amphiectosome tearing mechanism seemed relatively slow to me (over three minutes), and if this has been observed multiple times, it would be helpful to know if this is typical or whether there is considerable variation.

Thank you for this comment. In the revised manuscript, we highlight that the first released LC3 positive ILV was detected as early as within 40 sec.

Overall, I think the authors have been successful in identifying amphiectosomes secreted from multiple cell lines and demonstrating that the ILVs inside them have at least two origins (autophagosome membrane and late endosomal multivesicular body) based on the markers that they carry. The analysis of intracellular compartments producing these structures is rather less convincing and it remains unclear what cells release these structures in vivo.

I think there could be a significant impact on the EV field and consequently on our understanding of cell-cell signalling based on these findings. It will flag the importance of investigating the release of amphiectosomes in other studies, and although the authors do not discuss it, the molecular mechanisms involved in this type of 'ectosomal-style' release will be different from multivesicular compartment fusion to the plasma membrane and should be possible to be manipulated independently. Any experiments that demonstrate this would greatly strengthen the manuscript.

We appreciate these comments of the reviewer. Experiments are on their way to elucidate the mechanism of the “ectosomal style” exosome release and will be the topic of our next publication.

In general, the EV field has struggled to link up analysis of the subcellular biology of sEV secretion and the biochemical/physical analysis of the sEVs themselves, so from that perspective, the manuscript provides a novel angle on this problem.

Reviewer #3 (Public Review):

Summary:

In this manuscript, the authors describe a novel mode of release of small extracellular vesicles. These small EVs are released via the rupture of the membrane of so-called amphiectosomes that resemble "morphologically" Multivesicular Bodies.

These structures have been initially described by the authors as released by colorectal cancer cells (https://doi.org/10.1080/20013078.2019.1596668). In this manuscript, they provide experiments that allow us to generalize this process to other cells. In brief, amphiectosomes are likely released by ectocytosis of amphisomes that are formed by the fusion of multivesicular endosomes with autophagosomes. The authors propose that their model puts forward the hypothesis that LC3 positive vesicles are formed by "curling" of the autophagosomal membrane which then gives rise to an organelle where both CD63 and LC3 positive small EVs co-exist and would be released then by a budding mechanism at the cell surface that appears similar to the budding of microvesicles /ectosomes. Very correctly the authors make the distinction from migrasomes because these structures appear very similar in morphology.

Strengths:

The findings are interesting despite that it is unclear what would be the functional relevance of such a process and even how it could be induced. It points to a novel mode of release of extracellular vesicles.

Weaknesses:

This reviewer has comments and concerns concerning the interpretation of the data and the proposed model. In addition, in my opinion, some of the results in particular micrographs and immunoblots (even shown as supplementary data) are not of quality to support the conclusions.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) Highlight MV-IEV, ILV and limiting membrane in Figure-1G, N, and U.

Based on the suggestion, we revised Figure1

(2) Figure 1-Y-AF are not mentioned in the text.

In the revised manuscript, we discuss Figure 1Y-AF

(3) The term "IEVs" in Figure 2-S2 is not defined.

We modified the figure legend: we changed MV-lEV to amphiectosome

(4) Need to quantify co-localization in Figure 2-S2.

As suggested, we carried out the co-localisation analysis (Fig2-S2I), and Fig2-S2 was re-edited

Reviewer #2 (Recommendations For The Authors):

I have two recommendations for improving the manuscript through additional experiments:

(1) I think the description of the intracellular processes taking place in order to form amphiectosomes would be much stronger if some super-resolution imaging could be undertaken. This should label the different compartments before and after fusion with specific markers that highlight the protein signature of the different limiting and ILV membranes much more clearly than immuno-EM. It will also help in characterising the double-membrane structure of amphiectosomes at the point of budding and reveal whether the patchy labelling of the inner membrane emerges after amphiectosome release (the schematic model currently suggests that it happens before).

Thank you for your suggestion. STED microscopy was applied and results are shown in new Fig3 and the schematic model was modified accordingly.

(2) The implications of the manuscript would be more wide-ranging if the authors could test genetic manipulations that are believed to block exosome or ectosome release, eg. Rab27a or Arrdc1 knockdown. This may allow them to determine whether MV-lEVs can be released independently of the classical exosome release mechanism because they use a different route to be released from the plasma membrane. This experiment is not essential, but I think it would start to address the core regulatory mechanisms involved, and if successful, would easily allow the authors to determine the ratio of CD63-positive sEVs being secreted via classical versus amphiectosome routes.

The suggestion is very valuable for us and these studies are being performed in a separate project.

I think there are several other ways in which the manuscript could be improved to better explain some of the approaches, findings and interpretation:

(1) Include some explanation in the text of certain key tools, particularly:

a. Palm-GFP and whether its expression might alter the properties of the plasma membrane since this is used in a lot of experiments and is the only marker that seems to uniformly label the outer membrane of amphiectosomes. One concern might be that its expression drives amphiectosome secretion.

We found evidence for amphiectosome release also in the case of several different cells not expressing Palm-GFP. We believe, this excludes the possibility that Palm-GFP expression is the inducer of the amphiectosome release. Both by fluorescent and electron microscopy, the Palm-GFP non expressing cells showed very similar MV-lEVs. In addition, in the case of non-transduced HEK293 and fluorescent WGA-binding, we made similar observations.

b. Lactadherin - does this label the amphiectosomes after their release or does the wash-off step mean that it only labels cells, which subsequently release amphiectosomes?

Lactadherin labels the amphiectosomes after their release and fixation. Living cells cannot be labelled by lactadherin as PS is absent in the external plasma membrane layer of living cells. We used WGA on HEK293 cells to further support the plasma membrane origin of the external membrane of amphiectosomes.

(2) Explain the EM and confocal imaging approaches more clearly. Most importantly, is a 3D reconstruction always involved to confirm that 'separated' amphiectosomes are not joined to cells in another Z-plane.

Thank you for your suggestion. We have modified the manuscript accordingly

(3) Presenting triple-labelled images with red, green and yellow channels does not allow individual labelling to be determined without single-channel images and even then, it is much more informative to use three distinguishable colours that make a different colour with overlap, eg. CMY? Fig.2_S2D and E do not display individual channels, so definitely need to be changed.

In case of Fig.2_S2D, we now show the individual channels, the earlier E image has been removed. In case of the STED images, CMY colors had been used, as you suggested.

(4) Please discuss in the text the data in Figure 1Y onwards concerning single/double membranes on MV-lEVs.

In the revised manuscript, we discuss the question on single/double membranes and we refer to Figure 1Y-AF

(5) On line 162, reword 'intraluminal TSPAN4 only' to 'one in which TSPAN4 is only intraluminal' to make it clear that other proteins are also marking the intraluminal region, not TSPAN4 only.

We modified the text accordingly.

(6) Points for further discussion and further conclusions:

a. In vivo experiments - discuss the limitations of this part of the analysis - it seems that none of the amphiectosome markers have been analysed in this part of the study and the MV-lEVs are only in the circulation.

b. Can the authors give any further indication of the levels of MV-lEVs relative to free sEVs from any of their studies?

Using our current approach, it is not possible to determine the levels of MV-lEVs to free sEV. Without analyzing serial ultrathin sections, determination of the relative ratio of MV-lEVs and sEVs would depend on the actual section plane. In future projects, we will determine the ratio of LC3 positive and negative sEVs by single EV analysis techniques (such as SP-IRIS). In the revised manuscript, additional TEM images are included to provide evidence for the simultaneous presence of sEVs and MV-lEVs and MV-lEVs both inside and outside of the circulation.

c. Please discuss the single versus double membrane issue (relating to experiments proposed above).

We discuss this question in more details in the revised manuscript.

d. Please point out that the release mechanism (plasma membrane budding) will involve different molecular mechanisms to establish exosome release, and this might provide a route to determine relative importance.

We are currently running a systemic analysis of the release mechanism of amphiectosomes, and this will be the topic of a separate manuscript.

Reviewer #3 (Recommendations For The Authors):

* The model is not supported.

* The data is not of quality.

* The appropriate methods are not exploited.

We are sorry, we cannot respond to these unsupported critiques.

Author response:

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

eLife Assessment

This important study showing that sleep deprivation increases functional synapses while depleting silent synapses supports previous findings that excitatory signaling increases during wakefulness. This manuscript focuses in particular on AMPA/NMDA ratios. An interesting, although speculative, aspect of the manuscript is the inclusion of a model for the accumulation of sleep need that is based upon the MEF2C transcription factor but also links to the sleep-regulating SIK3-HDAC4/5 pathway. The authors have clarified some questions raised in the previous review, but the evidence for major claims was still found to be incomplete, requiring additional experimentation.

The major claims of this study are: 1) SD increases the AMPA/NMDA receptor ratio and RS restores it; 2) SD decreases silent synapses compared to CS and RS restores their number after SD; 3) the majority of SD-induced DEGs are found in ExIT cells (glutamate pyramidal neurons projecting within the telencephalon); 4) ExIT SD-induced DEGs are enriched for genes encoding synaptic shaping components and for autism spectrum disorder risk and; 5) these DEGs are also enriched for DEGs induced by Mef2c loss of function restricted to forebrain glutamate neurons (ExIT cells comprise a subset of these) and by over-expression of constitutively nuclear HDAC4 that represses MEF2c transcriptional function. The last claim is consistent with an intracellular signaling model (presented as a hypothesis to be tested, in figure 4B).

[The above is added to the start of the discussion section.]

The specific claims are supported by solid evidence provided in this manuscript. The statistical support is now more clearly presented, with several changes in response to queries by reviewer 1.

The technical issues raised by reviewer 1 do not detract from the claims, thus supported. The rationale for this assessment is expanded below in response to reviewer 1.

Summary:

This manuscript by Vogt et al examines how the synaptic composition of AMPA and NMDA receptors changes over sleep and wake states. The authors perform whole-cell patch clamp recordings to quantify changes in silent synapse number across conditions of spontaneous sleep, sleep deprivation, and recovery sleep after deprivation. They also perform single nucleus RNAseq to identify transcriptional changes related to AMPA/NMDA receptor composition following spontaneous sleep and sleep deprivation. The findings of this study are consistent with a decrease in silent synapse number during wakefulness and an increase during sleep. However, these changes cannot be conclusively linked to sleep/wake states. Measurements were performed in motor cortex, and sleep deprivation was achieved by forced locomotion, raising the possibility that recent patterns of neuronal activity, rather than sleep/wake states, are responsible for the observed results.

Strengths:

This study examines an important question. Glutamatergic synaptic transmission has been a focus of studies in the sleep field, but AMPA receptor function has been the primary target of these studies. Silent synapses, which contain NMDA receptors but lack AMPA receptors, have important functional consequences for the brain. Exploring the role of sleep in regulating silent synapse number is important to understanding the role of sleep in brain function. The electrophysiological approach of measuring the failure rate ratio, supported by AMPA/NMDA ratio measurements, is a rigorous tool to evaluate silent synapse number.

The authors also perform snRNAseq to identify genes differentially expressed in the spontaneous sleep and sleep deprivation groups. This analysis reveals an intriguing pattern of upregulated genes controlled by HDAC4 and Mef2c, along with synaptic shaping component genes and genes associated with autism spectrum disorder, across cell types in the sleep deprivation group. This unbiased approach identifies candidate genes for follow-up studies. The finding that ASD-risk genes are differentially expressed during SD also raises the intriguing possibility that normal sleep function is disrupted in ASD.

Weaknesses:

A major consideration to the interpretation of this study is the use of forced locomotion for sleep deprivation. Measurements are made from motor cortex, and therefore the effects observed could be due to differences in motor activity patterns across groups, rather than lack of sleep per se.

Experimentally induced lack of sleep always involves differences in motor activity. As previously noted in revision 1, motor learning is unlikely to occur in this paradigm and inspection of the video (in supplementary materials) shows no repetitive motor behavioral sequences during the sleep deprivation, nor can this be considered exercise due to the very slow speed of treadmill movement employed. The obvious major difference between groups is a lack of sleep per se. (See below in the “Recommendations for authors”, reviewer 1 for comments on localized wake activity inducing localized sleep-need responses)

Considering that other groups have failed to find a difference in AMPA/NMDA ratio in mice with different spontaneous sleep/wake histories (Bridi et al., Neuron 2020), confirmation of these findings in a different brain region would greatly strengthen the study.

The study of Bridi et al., Neuron 2020, is not comparable to our study for several important reasons. First, their compared groups were from different circadian phases (180 degrees out of phase), whereas in our study, the circadian times for each group were matched (ZT=6hours). Second, experimentally induced sleep loss did not occur whereas it was a focus of our study. Third, spontaneous sleep/wake cannot be accurately matched amongst subjects whereas in our study, sleep loss was matched exactly between groups.

We agree that assessment of AMPA/NMDA ratio and silent synapse number in sleep deprived compared to ad libitum sleep in other areas of the neocortex is of great interest and something we hope to pursue. It would not be surprising to find differences as preliminarily reported by Bahl, et al., Nat Commun. 2024 Jan 26;15(1):779. However, such data would not further strengthen our already well supported evidence for the differences we report in the motor cortex.

The electrophysiological measurements and statistical analyses raise several questions. Input resistance (cutoffs and actual values) are not provided, making it difficult to assess recording quality.

As stated in our first reply, these data were omitted (an admitted oversight on our part) but are now supplied in the methods section as, “Series resistance values for the recording pipette ranged between 8 and 15 MOhm and experiments with changes larger than 25% were not used for further analyses”. We have now also added the Rs/Rm (as a separate column) for each recorded neuron in table 1.

Parametric one-way ANOVAs were used, although the data do not appear to be normally distributed.

We have now removed all the One-way ANOVA tests for clarity (non-parametric tests were previously supplied in addition to the one-way ANOVA tests). Determination of significance with Kruskal-Wallis non-parametric test has not altered statistical support for our conclusions.

Reviewer 1 correctly points out that we had not tested for normality of our distributions- the distributions are likely to be normal but the sample size is too small to confidently make this call  for the ratio data which is why we removed the one-way ANOVA’s entirely from table 1.

Two-way ANOVA’s are used to assess AMPA and EPSC amplitudes and failure rates (table 1 tab 2&5)  across sleep conditions. As now indicated (table 1, tab 2&5), the distributions of AMPA and NMDA amplitudes and FRs passed the D'Agostino & Pearson test for normality and QQ plots provide illustration supporting this claim.

In addition, for the AMPA/NMDA and FRR measurements (Figures 1E, F), the SD group (rather than the control sleep group) was used as the control group for post-hoc comparisons, but it is unclear why.

The label of “control group” is arbitrary. CS and RS groups are similar (sleep density for RS>CS as expected).  Since this appears to be confusing, we now compare all groups to one another in table 1 with the same statistical outcome (additional comparison of CS to RS).

While the data appear in line with the authors' conclusions, the number of mice (3/group) and cells recorded is low, and adding more would better account for inter-animal variability and increase the robustness of the findings.

Of course, the larger the sample, the better the approximation to the population. Our sample sizes yielded significant differences at the usual p<=0.05 threshold with non-parametric testing. A larger sample size could allow for normality testing of the distributions of the data, but fortunately, this was not necessary to support our conclusions.

The snRNAseq data are intriguing. However, several genes relevant to the AMPA/NMDA ratio are mentioned, but the encoded proteins would be expected to have variable effects on AMPA/NMDA receptor trafficking and function, making the model presented in Figure 4C oversimplified. A more thorough discussion of the candidate genes and pathways that are upregulated during sleep deprivation, the spatiotemporal/posttranslational control of protein expression, and their effects on AMPA/NMDA trafficking vs function is warranted.

We have not studied the candidate genes at this point and do not yet understand their potential role(s) in sleep-related AMPA/NMDA functional ratio, only that their expression levels are altered with sleep condition. We agree with the reviewer that the data are intriguing and in need of further investigation. An important first step that can help direct such studies is the identification and preliminary characterization of good candidate genes with respect their cell type specificity, significance and fold change as we have done. Their potential roles likely depend on “the spatiotemporal/posttranslational control” and other factors as reviewer 1 notes.

Reviewer #2 (Public review):

Here Vogt et al., provide new insights into the need for sleep and the molecular and physiological response to sleep loss. The authors expand on their previously published work (Bjorness et al., 2020) and draw from recent advances in the field to propose a neuron-centric molecular model for the accumulation and resolution of sleep need and basis of restorative sleep function. While speculative, the proposed model successfully links important observations in the field and provides a framework to stimulate further research and advances on the molecular basis of sleep function. In my review, I highlight the important advances of this current work, the clear merits of the proposed model, and indicate areas of the model that can serve to stimulate further investigation.

Strengths:

Reviewer comment on new data in Vogt et al., 2024

Using classic slice electrophysiology, the authors conclude that wakefulness (sleep deprivation (SD)) drives a potentiation of excitatory glutamate synapses, mediated in large part by "un-silencing" of NMDAR-active synapses to AMPAR-active synapses. Using a modern single nuclear RNAseq approach the authors conclude that SD drives changes in gene expression primarily occurring in glutamatergic neurons. The two experiments combined highlight the accumulation and resolution of sleep need centered on the strength of excitatory synapses onto excitatory neurons. This view is entirely consistent with a large body of extant and emerging literature and provides important direction for future research.

Consistent with prior work, wakefulness/SD drives an LTP-type potentiation of excitatory synaptic strength on principle cortical neurons. It has been proposed that LTP associated with wake, leads to the accumulation of sleep need by increasing neuronal excitability, and by the "saturation" of LTP capacity. This saturation subsequently impairs the capacity for further ongoing learning. This new data provides a satisfying mechanism of this saturation phenomenon by introducing the concept of silent synapses. The new data show that in mice well rested, a substantial number of synapses are "silent", containing an NMDAR component but not AMPARs. Silent synapses provide a type of reservoir for learning in that activity can drive the un-silencing, increasing the number of functional synapses. SD depletes this reservoir of silent synapses to essentially zero, explaining how SD can exhaust learning capacity. Recovery sleep led to restoration of silent synapses, explaining how recovery sleep can renew learning capacity. In their prior work (Bjorness et al., 2020) this group showed that SD drives an increase in mEPSC frequency onto these same cortical neurons, but without a clear change in pre-synaptic release probability, implying a change in the number of functional synapses. This prediction is now born out in this new dataset.

The new snRNAseq dataset indicates the sleep need is primarily seen (at the transcriptional level) in excitatory neurons, consistent with a number of other studies. First, this conclusion is corroborated by an independent, contemporary snRNAseq analysis recently available as a pre-print (Ford et al., 2023 BioRxiv https://doi.org/10.1101/2023.11.28.569011). A recently published analysis on the effects of SD in drosophila imaged synapses in every brain region in a cell-type dependent manner (Weiss et al., PNAS 2024), concluding that SD drives brain wide increases in synaptic strength almost exclusively in excitatory neurons. Further, Kim et al., Nature 2022, heavily cited in this work, show that the newly described SIK3-HDAC4/5 pathway promotes sleep depth via excitatory neurons and not inhibitory neurons.

The new experiments provided in Fig1-3 are expertly conducted and presented. This reviewer has no comments of concern regarding the execution and conclusions of these experiments.

Reviewer comment on model in Vogt et al., 2024

To the view of this reviewer the new model proposed by Vogt et al., is an important contribution. The model is not definitively supported by new data, and in this regard should be viewed as a perspective, providing mechanistic links between recent molecular advances, while still leaving areas that need to be addressed in future work. New snRNAseq analysis indicates SD drives expression of synaptic shaping components (SSCs) consistent with the excitatory synapse as a major target for the restorative basis of sleep function. SD induced gene expression is also enriched for autism spectrum disorder (ASD) risk genes. As pointed out by the authors, sleep problems are commonly reported in ASD, but the emphasis has been on sleep amount. This new analysis highlights the need to understand the impact on sleep's functional output (synapses) to fully understand the role of sleep problems in ASD.

Importantly, SD induced gene expression in excitatory neurons overlap with genes regulated by the transcription factor MEF2C and HDAC4/5 (Fig. 4). In their prior work, the authors show loss of MEF2C in excitatory neurons abolished the SD transcriptional response and the functional recovery of synapses from SD by recovery sleep. Recent advances identified HDAC4/5 as major regulators of sleep depth and duration (in excitatory neurons) downstream of the recently identified sleep promoting kinase SIK3. In Zhou et al., and Kim et al., Nature 2022, both groups propose a model whereby "sleep-need" signals from the synapse activate SIK3, which phosphorylates HDAC4/5, driving cytoplasmic targeting, allowing for the de-repression and transcriptional activation of "sleep genes". Prior work shows that HDAC4/5 are repressors of MEF2C. Therefore, the "sleep genes" derepressed by HDAC4/5 may be the same genes activated in response to SD by MEF2C. The new model thereby extends the signaling of sleep need at synapses (through SIK3-HDAC4/5) to the functional output of synaptic recovery by expression of synaptic/sleep genes by MEF2C. The model thereby links aspects of expression of sleep need with the resolution of sleep need by mediating sleep function: synapse renormalization.

Weaknesses:

Areas for further investigation.

In the discussion section Vogt et al., explore the links between excitatory synapse strength, arguably the major target of "sleep function", and NREM slow-wave activity (SWA), the most established marker of sleep need. SIK3-HDAC4/5 have major effects on the "depth" of sleep by regulating NREM-SWA. The effects of MEF2C loss of function on NREM SWA activity are less obvious, but clearly impact the recovery of glutamatergic synapses from SD. The authors point out how adenosine signaling is well established as a mediator of SWA, but the links with adenosine and glutamatergic strength are far from clear. The mechanistic links between SIK3/HDAC4/5, adenosine signaling, and MEF2C, are far from understood. Therefore, the molecular/mechanistic links between a synaptic basis of sleep need and resolution with NREM-SWA activity require further investigation.

Additional work is also needed to understand the mechanistic links between SIK3-HDAC4/5 signaling and MEF2C activity. The authors point out that constitutively nuclear (cn) HDAC4/5 (acting as a repressor) will mimic MEF2C loss of function. This is reasonable, however, there are notable differences in the reported phenotypes of each. Notably, cnHDAC4/5 suppresses NREM amount and NREM SWA but had no effect on the NREM-SWA increase following SD (Zhou et al., Nature 2022).

We speculate that the effect of cnHDAC4/5 to reduce NREM-SWA together with the reduction of NREM amount may be due to a localized increase in neuronal excitability of arousal centers, which would be expected to mask NREM-SWA. Rebound NREM-SWA may reflect the relative rebound increase of NREM-SWA still present under chronic masking conditions (induced by cnHDAC4/5) of increased arousal system excitability. A similar effect to overcome NREM-SWA masking was reported in a Kcna2 KO mouse (a Shaker homologue) by Douglas, et al. (2007, BMC Biol).

Loss of MEF2C in CaMKII neurons had no effect on NREM amount and suppressed the increase in NREM-SWA following SD (Bjorness et al., 2020). These instances indicate that cnHDAC4/5 and loss of MEF2C do not exactly match suggesting additional factors are relevant in these phenotypes. Likely HDAC4/5 have functionally important interactions with other transcription factors, and likewise for MEF2C, suggesting areas for future analysis.

This is not a surprising outcome since both MEF2c and HDAC4/5 are transcription factors whose function(s) are determined by multiple other factors a subset of which are relevant to sleep conditions while other determining factors are not necessarily relevant to sleep. These factors can include their phosphorylation state, genomic accessibility, and interaction with other transcription factors. All these other factors are known to be both cell type specific and determined by intracellular conditions, that in turn, are affected by extracellular conditions and ligands. We certainly agree there is much future analysis needed.

One emerging theme may be that the SIK3-HDAC4/5 axis are major regulators of the sleep state, perhaps stabilizing the NREM state once the transition from wakefulness occurs. MEF2C is less involved in regulating sleep per se, and more involved in executing sleep function, by promoting restorative synaptic modifications to resolve sleep need.

A useful way to restate the above might be to distinguish between control of arousal levels determining the behavioral states, wake or sleep (including REM sleep) and control of sleep function. The term, sleep, is typically used to describe the behavioral state of sleep that acts as a permissive gate to sleep function (that resolves sleep need). The sleep state should not be conflated with sleep function. There is abundant evidence that control of arousal can be dissociated from sleep need and sleep function.

Finally, advances in the roles of the respective SIK3-HDAC4/5 and MEF2C pathways point towards transcription of "sleep genes", as clearly indicated in the model of Fig.4. Clearly more work is needed to understand how the expression of such genes ultimately lead to resolution of sleep need by functional changes at synapses.

We are in full agreement. We also note the SIK3-HDAC4/5 pathway may have more than one role, i.e., to affect arousal centers to alter behavioral state and, more generally, to control MEF2c’s transcriptional activity thus controlling sleep-related, glutamate, synaptic phenotype.

What are these sleep genes and how do they mechanistically resolve sleep need? Thus, the current work provides a mechanistic framework to stimulate further advances in understanding the molecular basis for sleep need and the restorative basis of sleep function.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Major comments:

(1) I appreciate the authors' thoughtful discussion of the use of forced locomotion for their sleep deprivation technique in their response, as well as the additional information that was provided regarding use of the treadmill in the manuscript. However, given that previous studies have failed to find a difference in AMPA/NMDA ratio following spontaneous sleep vs wake, confirmation of the findings in a non-motor brain region with the same SD technique (or confirmation within motor cortex with a different technique, although the authors correctly point out that other techniques also increase locomotor activity) would greatly strengthen the paper.

Addressed above

Notably, differences in motor activity patterns, not necessarily overall amount of locomotion, may induce differential synaptic changes between groups. This point at least warrants acknowledgement and discussion, but this has not been incorporated into the text of the manuscript.

We will incorporate the following into the discussion:

There is evidence that learning of a motor task  or experience of forced altered motor activity can result in localized increases in NREM (slow wave sleep)-slow wave activity (Huber R, Ghilardi MF, Massimini M, Tononi G. Local sleep and learning. Nature. 2004;430(6995):78-81); Huber et al., 2006) in the motor cortex. Since SWS-SWA is considered a marker for sleep homeostasis, the altered motor activity induced increase of SWS-SWA was considered evidence for sleep-related function. Our earlier work has clearly shown that the treadmill method of SD increases frontal cortical SWS-SWA rebound, indicating a sleep-homeostatic process (Bjorness et al., 2016; Bjorness et al., 2020). Furthermore, we have also shown that this means of experimental SD causes similar glutamate synaptic changes as those observed using other means of SD like gentle handling (Liu, et al., JoNS 2010).

(2) The number of mice and cells used for electrophysiology in this study remains low; more animals should be included to account for inter-animal variability.

For this study, increasing the number of mice and cells will have p<0.05 chance of altering our conclusions by rejecting the null hypotheses of the electrophysiology findings.

(3) The additional methodological information provided allays some of my concerns regarding the electrophysiological data. However, information about the input resistance (cutoffs used and/or actual values) is still not provided, which is important for assessing recording quality.

We have now supplied the experimentally determined input resistance for each neuron used in this study (a separate column in table 1, tabs marked, “data”).

(4) It is not meaningful to compare raw AMPA or NMDA responses because stimulus electrode placement will differ between cells, potentially activating different numbers of afferents. Presenting these comparisons (Figure 1C) has the potential to mislead the reader.

This is not misleading (it didn’t mislead reviewer 1) as we described the conditions. As expected by reviewer 1, the variability using “raw AMPA or NMDA responses…” was too great, but did indicate an interaction between receptor responses and sleep condition. This provided (as stated in the results section) rationale to examine, and to only draw conclusions from the AMPA/NMDA amplitude and FR ratios.

(5) I appreciate clarification on the statistics and the authors' response has answered some of my questions. However, this also raises additional questions. What test was used to determine normality (and therefore whether to perform a parametric vs nonparametrictest)?

Described above.

Why was the FRR data analysis changed to a parametric test, when it does not appear that the data are normally distributed?

Showing the parametric test was a mistake on our part- there are not enough samples to conclusively conclude the distributions are normal as reviewer 1 correctly suspects. However, the non-parametric Kruskal-Wallis tests that we also show  in table 1 indicate significant differences between conditions and the non-parametric, two-stage linear step-up procedure of Benjamini, Krieger and Yekutieli, indicates significant differences between CS-SD and RS-SD but not for CS-RS, supporting our conclusions. The (unsupported) parametric tests are now removed in Table 1 leaving behind the non-parametric test.

Why were post-hoc tests chosen to compare to a control group rather than all pairwise comparisons,

We now provide post-hoc all-pairwise comparisons to give the same results using the BKY analysis.

and why was the SD rather than CS group used as the control in Figures 1E and F?

Why were different post-hoc tests chosen for the data in Figures 1E, F?

There was no need for this and we now, only show statistics that are used to draw our conclusions for the AMPA/NMDA EPSC ratios data shown in Figure 1E and Failure Rate Ratios data shown in Figure 1F (the conclusions are supported by the non-parametric post-hoc test and remain unchanged).

(6) Genes in the SSC, ASD, Mef2cKO, and HD4cn categories are almost exclusively upregulated in the SD group compared to the CS group (Figure 4A). As the authors point out in their response, "No claim of mechanism linking the changed expression to altered AMPAR or NMDAR activity can be made at this point," largely due to the fact that we do not know the spatiotemporal or posttranslational modification patterns of the translated proteins, and how they affect receptor trafficking vs function. This is in agreement with my original point: as written (and as illustrated in Figure 4C), the manuscript implies that upregulation during SD increases the AMPA/NMDA ratio via receptor trafficking,

The model indicates a likely (but not necessarily exclusive) role for AMPA/NMDA trafficking to explain the functional electrophysiological data that we do report and which is not in dispute. The SSC-DEGs in ExIT cells are consistent with sleep-altered AMPA/NMDA trafficking but remain only a correlation. However, the point is taken and Figure 4c has been revised to only reflect what we have observed electrophysiologically and the speculated mechanism(s) mediated by observed SSC-DEGs are illustrated with “?’s”.

while in reality the picture is likely much more complicated, and therefore a more thorough discussion is warranted. Some discussion was provided in the authors' response but does not appear to have been incorporated into the text or Figure 4C.

As indicated above the proposed model is changed in Figure 4c to more explicitly indicate which aspects reflect our electrophysiological data and which aspects reflect only an association of observations. 

Minor comments:

(1) Please justify only using male mice

We had to start somewhere with our limited resources. Our intentions are to follow up with similar experiments using female mice, should funding be realized.

(2) The model in Figure 4C is oversimplified and remains problematic, for the reasons stated in comment #6, above.

See responses above.

(3) Figure 4D remains confusing

We agree. The unnecessary addition of adenosine effects on cholinergic arousal centers (experimentally well supported), have been removed from the figure to provide a more focused indication of how SWS-SWA can be related to either MEF2c and/or to ADORA1 activation through reduction of glutamate synaptic strength. ADORA1 activation elicits reduced glutamate synaptic activity through pre- and postsynaptic inhibition whereas MEF2c activation is essential to reduce sleep elicited, glutamate EPSC reduction. Reduced glutamate synaptic strength, whatever the cause, is associated with increased SWS-SWA.

Author response:

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

The study by Aguirre-Botero et al. shows the dynamics of 3D11 anti-CSP monoclonal antibody (mAb) mediated elimination of rodent malaria Plasmodium berghei (Pb) parasites in the liver. The authors show that the anti-CSP mAb could protect against intravenous (i.v.) Pb sporozoite challenge along with the cutaneous challenge, but requires higher concentration of antibody. Importantly, the study shows that the anti-CSP mAb not only affects sporozoite motility, sinusoidal extravasation, and cell invasion but also partially impairs the intracellular development inside the liver parenchyma, indicating a late effect of this antibody during liver stage development. While the study is interesting and conducted well, the only novel yet very important observation made in this manuscript is the effect of the anti-CSP mAb on liver stage development.

Major

This observation is highlighted in the manuscript title but is supported by only limited data. A such it needs to be substantiated and a mechanism should be investigated.  The phenomenon of intracellular effects of the anti-CSP mAb should be analyzed in much more detail. For example, can the authors demonstrate uptake of the Ab together with the parasite during hepatocyte invasion? What cellular mechanism leads to elimination?

Lines 234 - 243; 308 - 325: These results are the gist of the entire study and also defined the title of the manuscript. Thus, it would be pre-mature to claim the substantial effect of 3D11 antibody in late killing of the parasite in the infected hepatocytes just by looking at the decreased GFP fluorescence. The authors need to at least verify the fitness of the liver stages by measuring the size of the developing parasites as well as using different parasite specific markers (UIS4, MSP1, HSP70 etc.) in immunofluorescence assays on the infected liver sections and in vitro infections. 

We greatly appreciate the comments. We have taken the suggestions into consideration and deepened the characterization of 3D11's late killing of parasites. We first analyzed the presence of 3D11 in the intracellular parasite after the invasion and compared it with the CSP expression on the surface of control parasites (new Fig. 4F). Next, we tested a potential action of 3D11 added in the cell culture after the invasion (new Fig. 4G). The two new panels and the text accompanying them are shown below.

“Post-invasion labeling of 3D11 bound to the membrane of intracellular parasites revealed a strong staining surrounding the parasite at 2 and 15h, but only punctual traces of 3D11 at 44h (Figure 4F, 3D11, 3D11). Of note, CSP was detected surrounding the control parasites at all time-points indicating that the lack of staining at 44h is not due to a decrease in the CSP amount on the parasite surface (Figure 4F, CSP, Control).  To evaluate the potential post-invasion entry of 3D11 into the PV of infected cells and posterior neutralization of intracellular parasites, we incubated invaded cells from 2 to 44 h with 3D11, but no effect on the parasite intracellular development was observed (Figure 4G, 2h p.i.). 3D11 incubated for 2 h with sporozoites and cells elicited, as expected, a dose-dependent inhibition of parasite development. Altogether, our results indicate that the late inhibition of parasite development is already achieved at 15h and likely caused by antibodies dragged inside cells bound to sporozoites before or during the invasion.”

Finally, we better characterized the parasite loss of fitness caused by 3D11 in infected cells by quantifying the parasite size, GFP intensity and the presence and intensity of UIS4, a parasitophorous vacuole membrane developmental marker at 2, 4 and 44h as described below in the new figure 5 and accompanying text.

“To further characterize the killing of intracellular parasites by 3D11 in HepG2 cells, we next evaluated the expression of the parasitophorous vacuole membrane (PVM) marker, UIS4 37, to infer the parasite intracellular development at 2, 4 and 44h. HepG2 cells were incubated with Pb-GFP expressing sporozoites in the absence (Control, Figure 5) or presence of 1.25 µg/mL of 3D11 during the first two hours of incubation (3D11, Figure 5). The chosen 3D11 concentration led to ~50% decrease in cell invasion (Figure 4C, 2h) and ~30% decrease in the post-invasion number of EEFs (Figure 4D), leaving enough parasites to be analyzed by microscopy. To distinguish between extracellular and intracellular parasites at 2h, washed and fixed samples were incubated with mouse 3D11 mAb (1µg/mL) and revealed with a fluorescent anti-mouse secondary antibody (Figure 5A, 3D11 in blue). Samples were then permeabilized and incubated with a goat anti-UIS4 polyclonal antibody revealed with a fluorescent anti-goat secondary antibody (Figure 5A, UIS4 in red). DNA was stained with Hoechst (Figure 5A, DNA in white).

Extracellular GFP+ sporozoites were identified by their 3D11+UIS4- phenotype (Figure 5A, 2h, extracellular). Conversely, intracellular parasites were identified by their 3D11- phenotype and stained positive or negative for UIS4 (Figure 5A, 2h and 44h, intracellular). UIS4+ PVM is normally associated with a productive cell infection 37. However, a small number of EEFs can develop in the absence of UIS4 37, likely inside the host cell nucleus (Figure 5A, 44h, intranuclear).

In the control and 3D11-treated groups, the percentage of intracellular UIS4- parasites decreased 2 to 3-fold from 2 to 44h, as expected of a parasite population negative for a marker of productive infection (Figure 5B). However, while at 2h in the control group, this population represented 14% of intracellular parasites, in the 3D11-treated group, it reached 48% (Figure 5B). This ~3-fold increase in the UIS4 negative population could explain the late killing of intracellular sporozoites by 3D11. Whether this population is constituted by intracellular transmigratory sporozoites lacking a PVM or parasites surrounded by a PVM, but incapable of secreting UIS4 still needs to be determined. At 44h, surviving EEFs in the 3D11-treated samples presented a similar area and UIS4 staining intensity than control parasites (Figure 5C, D). However, as observed by flow cytometry (Figure 4D), the GFP intensity of 3D11-treated parasites was significantly lower than control EEFs, indicating that 3D11 can somehow affect protein expression with undetermined effects in the genesis of red blood cell infecting stages.”

Minor<br /> • Line 44 - 43: The statement is applicable only to the rodent infecting Plasmodium parasites. The authors need to clarify that.

This is an important clarification. We have modified the text that now reads:

“The sporozoite surface is covered by a dense coat of the circumsporozoite protein (CSP), shown to be an immunodominant protective antigen using a rodent malaria model”

• Line 68: Replace the second 'against' after the CSP with 'of'.

It is done.

• Line 141 - 143: The 3D11 mAb does affect the homing and killing in the blood of cutaneous injected sporozoites. The authors need to clearly state that the statement is true only for i.v. injected sporozoites.

Thank you for the comment. Now the text reads:

“Altogether, these data indicate that 3D11 rather than having an early effect on i.v. inoculated sporozoites in the blood circulation, e.g. by inhibiting the homing or killing the parasite in the blood, requires more than 4 h to eliminate most parasites in the liver.”

• Figure 3B: The numbers of sporozoites detected in the experiment varies from 0 h (line 172) to 2 h (line 184). Therefore, the numbers need to be mentioned on all the bars of each timepoint.

We have now added the numbers at the top of the graph from Figure 3B.

• Figure 3C: If the authors have used flk1-GFP mice, then how well they were able to detect the Pb-PfCSP GFP parasites in the vessel vs. parenchyma in the intravital imaging? The representative images for Pb-PfCSP GFP should also be included.

Since 3D11 does not target PbPf parasites most of them are motile in the movies, making them easily distinguishable from the endothelial cells. In addition, the stronger GFP intensity of sporozoites makes them detectable in the sinusoids. Representative images were added in the new Figure S3.

• It is not mentioned anywhere how the viability of the sporozoites was determined. This has to be described especially in the methods section.

• Also, the flow acquisition and data analysis of the sporozoites and infected HepG2 cells must be described in the method section.

We briefly mentioned it in the results (line 228- 230): “In addition, by comparing the total number of recovered GFP+ sporozoites at 2 h in the two studied conditions, we measured the early lethality (%viable sporozoites, Figure 4B) of the anti-CSP Ab on the extracellular forms of the parasite (Figure 4A).”

A more detailed description has been added in the methods section that now reads:

“After 2 h, the supernatant was collected, and the culture was washed 2x with 0.5 volume of PBS. The cells were subsequently trypsinized. The supernatant plus the washing steps and the trypsinized cells were analyzed by flow cytometry to quantify the amount of GFP+ events inside and outside cells (Figure 3A and Figure S4). Viability was then quantified by the sum of the total number of sporozoites (GPF+ events) in the supernatant, inside and outside the cells. We calculated the percentage of parasite viability by dividing the average of the total number of sporozoites in the treated samples by the average in controls using three technical replicates for each condition. Additionally, we quantified the percentage of infected cells using the total number of GFP+ events in the HepG2 gate (Figure S4). To compare the biological replicates, we further normalized to the control of each experiment. For the samples used to analyze parasite development, the cells were incubated for 15 or 44 h after sporozoite addition, and the medium was changed after 2 and 24 h. The cells were trypsinized and the percentage of intracellular parasites was determined by flow cytometry as described above (Figure S4). The prolonged effect between 2 h and 15/44 h was calculated by normalizing the percentage of infected cells at 15/44 h to that of 2 h. For all flow cytometry measurements, the same volume was acquired.”

• Figure 4: The flow layouts should be included for at least comparing the 0 vs. 5 μg/ml of 3D11 mAb concentrations.

Flow layouts were added in the supplementary figure 4.

• Line 651 (Figure S1 legend): Typographical error '14'.

Thank you for noticing. We corrected it.

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

Aguirre-Botero and collaborators report on the dynamics of Plasmodium parasite elimination in the liver using the 3D11 anti-CSP monoclonal antibody (mAb). By using microscopy and bioluminescence imaging in the P. berghei rodent malaria model, the authors first demonstrate that higher antibody concentrations are required for protection against intravenous sporozoite challenge, when compared to cutaneous challenge, which is not surprising. The study also shows that the 3D11 mAb reduces sporozoite motility, impairs hepatic sinusoidal barrier crossing, and more relevantly inhibits intracellular development of liver stages through its cytotoxic activity. These findings highlight the role of this specific monoclonal antibody, 3D11 mAb against CSP, in targeting sporozoites in the liver.
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Major Comments

The study provides valuable insights into the mechanisms of protection conferred by the 3D11 anti-CSP monoclonal antibody against P. berghei sporozoites and this finding allow the field to speculate that other monoclonal antibodies against CSP of P. Falciparum may act similarly. However, an important experiment is missing that would significantly strengthen the conclusions. Specifically, the authors should perform experiments where the monoclonal antibody is added immediately after the sporozoites have completed invasion. This should be done both in vitro and in vivo to show whether the antibody has any effect on intracellular development of liver stages when added after invasion.

While the claims are generally supported by the data presented, to comprehensively conclude the late cytotoxic effects of 3D11, the additional experiment of post-invasion antibody application is relevant. This would help determine if the observed effects are due to the antibody's action during invasion or its continued action post-invasion.

The data and methods are presented in a manner that allows for reproducibility. The use of microscopy and bioluminescence imaging is well-documented. The experiments appear adequately replicated, and statistical analyses are appropriate.

We thank reviewer 2 for these important suggestions. To be sure that the effect might not come from the internalization of the antibodies after sporozoite invasion, we tested the amount of 3D11 bound to the parasite following invasion (new Fig. 4F) and the potential post-invasion neutralizing effect of 3D11 in vitro. The results obtained are presented below.

“Post-invasion labeling of 3D11 bound to the membrane of intracellular parasites revealed a strong staining surrounding the parasite at 2 and 15h, but only punctual traces of 3D11 at 44h (Figure 4F, 3D11, 3D11). Of note, CSP was detected surrounding the control parasites at all time-points indicating that the lack of staining at 44h is not due to a decrease in the CSP amount on the parasite surface (Figure 4F, CSP, Control).  To evaluate the potential post-invasion entry of 3D11 into the PV of infected cells and posterior neutralization of intracellular parasites, we incubated invaded cells from 2 to 44 h with 3D11, but no effect on the parasite intracellular development was observed (Figure 4G, 2h p.i.). 3D11 incubated for 2 h with sporozoites and cells elicited, as expected, a dose-dependent inhibition of parasite development. Altogether, our results indicate that the late inhibition of parasite development is already achieved at 15h and likely caused by antibodies dragged inside cells bound to sporozoites before or during the invasion.”

Minor Comments

The text and figures are clear and accurate. Some minor typographical errors should be corrected.

Thank you for the remark; we have verified the text again to remove typographical errors.

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

Aguirre-Botero et al have studied the effect of a potent monoclonal antibody against the circumsporozoite protein, the major surface protein of the malaria sporozoite. This is an elegantly designed, performed, and analyzed study. They have efficiently delineated the mode of action of anti-CSP repeat mAb and confirmed previous in vitro work (not cited) that demonstrated the same intracellular effect. 

Specific comments

Line 51: The authors claim a correlation between high antibody levels and protection. However, they did not provide direct proof that these antibodies were responsible for protection, nor did they establish a cut-off level of anti-CSP antibodies that would distinguish between protected and unprotected individuals.

We thank reviewer 3 for the comments. Indeed, we agree with reviewer 3, these are correlative studies where the causality cannot be established. We modified the ensuing sentence to specify the causality between anti-CSP mAbs and in vivo protection against sporozoite infection. Now the text reads:

“Extensive research has demonstrated a positive correlation between high levels of anti-CSP antibodies (Abs) induced by the RTS,S/AS01 vaccine and efficacy against malaria(11-13). Remarkably, anti-CSP monoclonal Abs (mAbs) have been proven to protect in vivo against malaria in various experimental settings, including, mice(14-21), monkeys(23), and humans(24-26)”

Line 326: The late intrahepatic effect of mAb against the CSP repeat has been previously reported (see Figure 2, Nudelman et al, J Immunol, 1989). The effect was shown to affect the transition from liver trophozoites to liver schizonts. This study should be cited and discussed.

Thank you for this important remark. We included this seminal reference and now the modified text reads:

“Notably, a similar effect has been previously reported using sera from mice immunized with PfCSP or mAb against P. yoelii (Py) CSP. Incubation of Pf or Py sporozoites with the immune sera or mAbs not only affected sporozoite invasion in vitro but continued to affect intracellular forms for several days after invasion(38,39). Additionally, using anti-PfCSP sera, it was also observed that late EEFs from sera-treated sporozoites had abnormal morphology(38). Altogether, it was thus concluded that the anti-CSP Abs present in the sera had a long-term effect on the parasites(38,39).”

Author response:

Public Reviews:

Reviewer #1 (Public review):

Summary:

This manuscript by Kaya et al. studies the effect of food consumption on hippocampal sharp wave ripples (SWRs) in mice. The authors use multiple foods and forms of food delivery to show that the frequency and power of SWRs increase following food intake, and that this effect depends on the caloric content of food. The authors also studied the effects of the administration of various food-intake-related hormones on SWRs during sleep, demonstrating that ghrelin negatively affects SWR rate and power, but not GLP-1, insulin, or leptin. Finally, the authors use fiber photometry to show that GABAergic neurons in the lateral hypothalamus, increase activity during a SWR event.

Strengths:

The experiments in this study seem to be well performed, and the data are well presented, visually. The data support the main conclusions of the manuscript that food intake enhances hippocampal SWRs. Taken together, this study is likely to be impactful to the study of the impact of feeding on sleep behavior, as well as the phenomena of hippocampal SWRs in metabolism.

Weaknesses:

Details of experiments are missing in the text and figure legends. Additionally, the writing of the manuscript could be improved.

We thank the reviewer for their favorable assessment of the work and its potential impact. We will add all requested details in the text and figure legends and will revise the wording of the manuscript to improve its clarity.

Reviewer #2 (Public review):

Summary:

Kaya et al uncover an intriguing relationship between hippocampal sharp wave-ripple production and peripheral hormone exposure, food intake, and lateral hypothalamic function. These findings significantly expand our understanding of hippocampal function beyond mnemonic processes and point a direction for promising future research.

Strengths:

Some of the relationships observed in this paper are highly significant. In particular, the inverse relationship between GLP1/Leptin and Insulin/Ghrelin are particularly compelling as this aligns well with opposing hormone functions on satiety.

Weaknesses:

I would be curious if there were any measurable behavioral differences that occur with different hormone manipulations.

We thank the reviewer for their favorable assessment of the work and its contribution to our understanding of non-mnemonic hippocampal function. Whether there are behavioral differences that occur following administration of the different hormones is a great question, yet unfortunately our study design did not include fine behavioral monitoring to the degree that would allow answering it. While some previous studies have partially addressed the behavioral consequences of the delivery of these hormones (we will include a reference to these studies in the revised manuscript), how these changes may interact with the hippocampal and hypothalamic effects we observe is a very interesting next step.

Reviewer #3 (Public review):

Summary:

The manuscript by Kaya et al. explores the effects of feeding on sharp wave-ripples (SWRs) in the hippocampus, which could reveal a better understanding of how metabolism is regulated by neural processes. Expanding on prior work that showed that SWRs trigger a decrease in peripheral glucose levels, the authors further tested the relationship between SWRs and meal consumption by recording LFPs from the dorsal CA1 region of the hippocampus before and after meal consumption. They found an increase in SWR magnitude during sleep after food intake, in both food restricted and ad libitum fed conditions. Using fiber photometry to detect GABAergic neuron activity in the lateral hypothalamus, they found increased activity locked to the onset of SWRs. They conclude that the animal's satiety state modulates the amplitude and rate of SWRs, and that SWRs modulate downstream circuits involved in regulating feeding. These experiments provide an important step forward in understanding how metabolism is regulated in the brain. However, currently, the paper lacks sufficient analyses to control for factors related to sleep quality and duration; adding these analyses would further support the claim that food intake itself, as opposed to sleep quality, is primarily responsible for changes in SWR activity. Adding this, along with some minor clarifications and edits, would lead to a compelling case for SWRs being modulated by a satiety state. The study will likely be of great interest in the field of learning and memory while carrying broader implications for understanding brain-body physiology.

Strengths:

The paper makes an innovative foray into the emerging field of brain-body research, asking how sharp wave-ripples are affected by metabolism and hunger. The authors use a variety of advanced techniques including LFP recordings and fiber photometry to answer this question. Additionally, they perform comprehensive and logical follow-up experiments to the initial food-restricted paradigm to account for deeper sleep following meal times and the difference between consumption of calories versus the experience of eating. These experiments lay the groundwork for future studies in this field, as the authors pose several follow-up questions regarding the role of metabolic hormones and downstream brain regions.

We thank the reviewer for their appreciation and constructive review of the work.

Weaknesses:

Major comments:

(1) The authors conclude that food intake regulates SWR power during sleep beyond the effect of food intake on sleep quality. Specifically, they made an attempt to control for the confounding effect of delta power on SWRs through a mediation analysis. However, a similar analysis is not presented for SWR rate. Moreover, this does not seem to be a sufficient control. One alternative way to address this confound would be to subsample the sleep data from the ad lib and food restricted conditions (or high calorie and low calorie, etc), to match the delta power in each condition. When periods of similar mean delta power (i.e. similar sleep quality) are matched between datasets, the authors can then determine if a significant effect on SWR amplitude and rate remains in the subsampled data.

This is an important point that we believe we addressed in a few complementary ways. First, the mediation analysis we implemented measures the magnitude and significance of the contribution of food on SWR power after accounting for the effects of delta power, showing a highly significant food-SWR contribution. While the objective of subsampling is similar, mediation is a more statistically robust approach as it models the relationship between food, SWR power, and delta power in a way that explicitly accounts for the interdependence of these variables. Further, subsampling introduces the risk of losing statistical power by reducing the sample size, due to exclusion of data that might contain relevant and valuable information. Mediation analysis, on the other hand, uses the full dataset and retains statistical power while modeling the relationships between variables more holistically. However, as we were not satisfied with a purely analytical approach to test this issue, we carried out a new set of experiments in ad-libitum fed mice, where there is no potential issue of food restriction impairing sleep quality in the pre-sleep session. In these conditions food amount also significantly correlated with, and showed significant mediation of, the SWR power change. Finally, we acknowledge and discuss this point in the Discussion, highlighting that given the known relationship between cortical delta and SWRs, it is challenging to fully disentangle these signals.

(2) Relatedly, are the animals spending the same amount of time sleeping in the ad lib vs. food restricted conditions? The amount of time spent sleeping could affect the probability of entering certain stages of sleep and thus affect SWR properties. A recent paper (Giri et al., Nature, 2024) demonstrated that sleep deprivation can alter the magnitude and frequency of SWRs. Could the authors quantify sleep quantity and control for the amount of time spent sleeping by subsampling the data, similar to the suggestion above?

We will include a comparison of sleep amount in the revised manuscript.

Additionally, we will add details to the Methods section that were missing in the original submission that are relevant to this point. Specifically, within the sleep sessions, the ongoing sleep states were scored using the AccuSleep toolbox (https://github.com/zekebarger/AccuSleep) using the EEG and EMG signals. NREM periods were detected based on high EEG delta power and low EMG power, REM periods were detected based on high EEG theta power and low EMG power, and Wake periods were detected based on high EMG power. Importantly, only NREM periods were included for subsequent SWR detection, quantification and analyses (in particular, reported SWR rates reflect the number of SWRs per second of NREM sleep).

(3) Plot 5I only reports significance but does not clearly show the underlying quantification of LH GABAergic activity. Upon reading the methods for how this analysis was conducted, it would be informative to see a plot of the pre-SWR and post-SWR integral values used for the paired t-test whose p-values are currently shown. For example, these values could be displayed as individual points overlaid on a pair of box-and-whisker plots of the pre- and post-distribution within the session (perhaps for one example session per mouse with the p-value reported, to supplement a plot of the distribution of p-values across sessions and mice). If these data are non-normal, the authors should also use a non-parametric statistical test.

We will include this quantification and visual representation in the revised manuscript.

Minor comments:

(4) A brief explanation (perhaps in the discussion) of what each change in SWR property (magnitude, rate, duration) could indicate in the context of the hypothesis may be helpful in bridging the fields of metabolism and memory. For example, by describing the hypothesized mechanistic consequence of each change, could the authors speculate on why ripple rate may not increase in all the instances where ripple power increases after feeding? Why do the authors speculate that ripple duration does not increase, given that prior work (Fernandez-Ruiz et al. 2019) has shown that prolonged ripples support enhanced memory?

We will include a discussion of these points in the revised manuscript.

(5) The authors suggest that "SWRs could modulate peripheral metabolism" as a future implication of their work. However, the lack of clear effects from GLP-1, leptin and insulin complicates this interpretation. It might be informative for readers if the authors expanded their discussion of what specific role they speculate that SWRs could play in regulating metabolism, given these negative results.

While we provided potential explanations for the lack of effects of the hormone administrations, we will further elaborate on this point in the revised manuscript.

Author response:

Public Reviews: 

Reviewer #1 (Public review): 

Summary: <br /> In this manuscript, the authors identified that 

(1) CDK4/6i treatment attenuates the growth of drug-resistant cells by prolongation of the G1 phase; 

(2) CDK4/6i treatment results in an ineffective Rb inactivation pathway and suppresses the growth of drug-resistant tumors;

(3) Addition of endocrine therapy augments the efficacy of CDK4/6i maintenance;

(4) Addition of CDK2i with CDK4/6 treatment as second-line treatment can suppress the growth of resistant cell;

(5) The role of cyclin E as a key driver of resistance to CDK4/6 and CDK2 inhibition.

Strengths:

To prove their complicated proposal, the authors employed orchestration of several kinds of live cell markers, timed in situ hybridization, IF and Immunoblotting. The authors strongly recognize the resistance of CDK4/6 + ET therapy and demonstrated how to overcome it.

Weaknesses:

The authors need to underscore their proposed results from what is to be achieved by them and by other researchers. 

Thank you for your thoughtful review and for highlighting both the strengths and weaknesses of our manuscript. We appreciate your recognition of the methodological rigor and the significance of our findings in addressing resistance to CDK4/6 inhibitors combined with endocrine therapy.

To address your concern regarding the need to delineate our results from those achieved by other researchers, we will incorporate clarifications in the revised manuscript. Specifically, we will:

(1) Clearly distinguish our novel contributions from prior findings in the field.

(2) Explicitly cite and discuss relevant studies to contextualize our work, ensuring that our contributions are appropriately framed within the broader body of knowledge.

These revisions will enhance the transparency and impact of our manuscript, as well as highlight the originality and significance of our findings. Thank you again for your constructive feedback.

Reviewer #2 (Public review):

Summary:

This study elucidated the mechanism underlying drug resistance induced by CDK4/6i as a single agent and proposed a novel and efficacious second-line therapeutic strategy. It highlighted the potential of combining CDK2i with CDK4/6i for the treatment of HR+/HER2- breast cancer.

Strengths:

The study demonstrated that CDK4/6 induces drug resistance by impairing Rb activation, which results in diminished E2F activity and a delay in G1 phase progression. It suggests that the synergistic use of CDK2i and CDK4/6i may represent a promising second-line treatment approach. Addressing critical clinical challenges, this study holds substantial practical implications.

Weaknesses: 

(1) Drug-resistant cell lines: Was a drug concentration gradient treatment employed to establish drug-resistant cell lines? If affirmative, this methodology should be detailed in the materials and methods section. 

We greatly appreciate the reviewer for raising this important question. In the revised manuscript, we will update the methods section to include a detailed description of how the drug-resistant cell lines were developed. Specifically, we will clarify whether a drug concentration gradient treatment was employed and provide step-by-step details to ensure reproducibility.

(2) What rationale informed the selection of MCF-7 cells for the generation of CDK6 knockout cell lines? Supplementary Figure 3. A indicates that CDK6 expression levels in MCF-7 cells are not notably elevated. 

We appreciate the reviewer’s insightful question about the rationale for selecting MCF-7 cells to generate CDK6 knockout cell lines. This choice was guided by prior studies highlighting the significant role of CDK6 in mediating resistance to CDK4/6 inhibitors (1-4). Moreover, we observed a 4.6-fold increase in CDK6 expression in CDK4/6 inhibitor-resistant MCF-7 cells compared to their drug-naïve counterparts (Supplementary Figure 3A). While we did not detect notable differences in CDK4/6 activity between wild-type and CDK6 knockout cells under CDK4/6 inhibitor treatment, these findings point to a potential non-canonical function of CDK6 in conferring resistance to CDK4/6 inhibitors.

(3) For each experiment, particularly those involving mice, the author must specify the number of individuals utilized and the number of replicates conducted, as detailed in the materials and methods section. 

We sincerely thank the reviewer for bringing this to our attention. In the revised manuscript, we will provide explicit details regarding the number of replicates and mice used for each experiment. This information will be included in the materials and methods section, figure legends, and relevant text to ensure transparency and clarity.

(4) Could this treatment approach be extended to triple-negative breast cancer? 

We greatly appreciate the reviewer’s inquiry about extending our findings to triple-negative breast cancer (TNBC). Based on our data presented in Figure 1 and Supplementary Figure 2, which include the TNBC cell line MDA-MB-231, we anticipate that the benefits of maintaining CDK4/6 inhibitors could indeed be applied to TNBC with an intact Rb/E2F pathway.

Reviewer #3 (Public review):

Summary:

In their manuscript, Armand and colleagues investigate the potential of continuing CDK4/6 inhibitors or combining them with CDK2 inhibitors in the treatment of breast cancer that has developed resistance to initial therapy. Utilizing cellular and animal models, the research examines whether maintaining CDK4/6 inhibition or adding CDK2 inhibitors can effectively control tumor growth after resistance has set in. The key findings from the study indicate that the sustained use of CDK4/6 inhibitors can slow down the proliferation of cancer cells that have become resistant, and the combination of CDK2 inhibitors with CDK4/6 inhibitors can further enhance the suppression of tumor growth. Additionally, the study identifies that high levels of Cyclin E play a significant role in resistance to the combined therapy. These results suggest that continuing CDK4/6 inhibitors along with the strategic use of CDK2 inhibitors could be an effective strategy to overcome treatment resistance in hormone receptor-positive breast cancer.

Strengths:

(1) Continuous CDK4/6 Inhibitor Treatment Significantly Suppresses the Growth of Drug-Resistant HR+ Breast Cancer: The study demonstrates that the continued use of CDK4/6 inhibitors, even after disease progression, can significantly inhibit the growth of drug-resistant breast cancer.

(2) Potential of Combined Use of CDK2 Inhibitors with CDK4/6 Inhibitors: The research highlights the potential of combining CDK2 inhibitors with CDK4/6 inhibitors to effectively suppress CDK2 activity and overcome drug resistance.

(3) Discovery of Cyclin E Overexpression as a Key Driver: The study identifies overexpression of cyclin E as a key driver of resistance to the combination of CDK4/6 and CDK2 inhibitors, providing insights for future cancer treatments.

(4) Consistency of In Vitro and In Vivo Experimental Results: The study obtained supportive results from both in vitro cell experiments and in vivo tumor models, enhancing the reliability of the research.

(5) Validation with Multiple Cell Lines: The research utilized multiple HR+/HER2- breast cancer cell lines (such as MCF-7, T47D, CAMA-1) and triple-negative breast cancer cell lines (such as MDA-MB-231), validating the broad applicability of the results.

Weaknesses:

(1) The manuscript presents intriguing findings on the sustained use of CDK4/6 inhibitors and the potential incorporation of CDK2 inhibitors in breast cancer treatment. However, I would appreciate a more detailed discussion of how these findings could be translated into clinical practice, particularly regarding the management of patients with drug-resistant breast cancer. 

We greatly appreciate this opportunity to further contextualize our findings within clinical practice. In the revised manuscript, we will expand the discussion to explore how the identified mechanisms can inform patient stratification and therapeutic combinations. We will also highlight the potential of integrating CDK2 inhibitors with continued CDK4/6 inhibition as a second-line strategy for HR+ breast cancer patients who exhibit resistance to CDK4/6 inhibitors, leveraging insights from current and ongoing clinical trials. This will provide a clearer framework for translating our findings into actionable therapeutic strategies.

(2) While the emergence of resistance is acknowledged, the manuscript could benefit from a deeper exploration of the molecular mechanisms underlying resistance development. A more thorough understanding of how CDK2 inhibitors may overcome this resistance would be valuable. 

Thank you for this insightful suggestion. In the revised manuscript, we will delve deeper into the molecular mechanisms by which CDK2 inhibitors counteract resistance to CDK4/6 inhibitors and endocrine therapy. We will emphasize the role of the non-canonical Rb inactivation pathway and upregulated transcriptional activity in reactivating CDK2, which contribute to resistance under CDK4/6 inhibition. Furthermore, we will discuss how dual inhibition of CDK4/6 and CDK2 effectively suppresses this resistance pathway, offering a mechanistic rationale for the therapeutic potential of this combination strategy.

(3) The manuscript supports the continued use of CDK4/6 inhibitors, but it lacks a discussion on the long-term efficacy and safety of this approach. Additional studies or data to support the safety profile of prolonged CDK4/6 inhibitor use would strengthen the manuscript. 

We greatly appreciate the reviewer for raising this important point. To address this, we will incorporate a discussion on the long-term safety and efficacy of CDK4/6 inhibitor maintenance therapy. Drawing from clinical trials and retrospective analyses (5-9), we will highlight data supporting the tolerability of prolonged CDK4/6i treatment, particularly in combination with endocrine therapy. We will also discuss its clinical benefits over chemotherapy or endocrine therapy alone, contextualizing these findings with our proposed therapeutic approach (6,8-11).

References:

(1) Yang C, Li Z, Bhatt T, Dickler M, Giri D, Scaltriti M_, et al._ Acquired CDK6 amplification promotes breast cancer resistance to CDK4/6 inhibitors and loss of ER signaling and dependence. Oncogene 2017;36:2255-64

(2) Li Q, Jiang B, Guo J, Shao H, Del Priore IS, Chang Q_, et al._ INK4 Tumor Suppressor Proteins Mediate Resistance to CDK4/6 Kinase Inhibitors. Cancer Discov 2022;12:356-71

(3) Ji W, Zhang W, Wang X, Shi Y, Yang F, Xie H_, et al._ c-myc regulates the sensitivity of breast cancer cells to palbociclib via c-myc/miR-29b-3p/CDK6 axis. Cell Death & Disease 2020;11:760

(4) Wu X, Yang X, Xiong Y, Li R, Ito T, Ahmed TA_, et al._ Distinct CDK6 complexes determine tumor cell response to CDK4/6 inhibitors and degraders. Nature Cancer 2021;2:429-43

(5) Martin JM, Handorf EA, Montero AJ, Goldstein LJ. Systemic Therapies Following Progression on First-line CDK4/6-inhibitor Treatment: Analysis of Real-world Data. Oncologist 2022;27:441-6

(6) Xi J, Oza A, Thomas S, Ademuyiwa F, Weilbaecher K, Suresh R_, et al._ Retrospective Analysis of Treatment Patterns and Effectiveness of Palbociclib and Subsequent Regimens in Metastatic Breast Cancer. J Natl Compr Canc Netw 2019;17:141-7

(7) Basile D, Gerratana L, Corvaja C, Pelizzari G, Franceschin G, Bertoli E_, et al._ First- and second-line treatment strategies for hormone-receptor (HR)-positive HER2-negative metastatic breast cancer: A real-world study. Breast 2021;57:104-12

(8) Kalinsky K, Accordino MK, Chiuzan C, Mundi PS, Sakach E, Sathe C_, et al._ Randomized Phase II Trial of Endocrine Therapy With or Without Ribociclib After Progression on Cyclin-Dependent Kinase 4/6 Inhibition in Hormone Receptor–Positive, Human Epidermal Growth Factor Receptor 2–Negative Metastatic Breast Cancer: MAINTAIN Trial. Journal of Clinical Oncology;0:JCO.22.02392

(9) Kalinsky K, Bianchini G, Hamilton EP, Graff SL, Park KH, Jeselsohn R_, et al._ Abemaciclib plus fulvestrant vs fulvestrant alone for HR+, HER2- advanced breast cancer following progression on a prior CDK4/6 inhibitor plus endocrine therapy: Primary outcome of the phase 3 postMONARCH trial. Journal of Clinical Oncology 2024;42:LBA1001-LBA

(10) Mayer EL, Wander SA, Regan MM, DeMichele A, Forero-Torres A, Rimawi MF_, et al._ Palbociclib after CDK and endocrine therapy (PACE): A randomized phase II study of fulvestrant, palbociclib, and avelumab for endocrine pre-treated ER+/HER2- metastatic breast cancer. Journal of Clinical Oncology 2018;36:TPS1104-TPS

(11) Llombart-Cussac A, Harper-Wynne C, Perello A, Hennequin A, Fernandez A, Colleoni M_, et al._ Second-line endocrine therapy (ET) with or without palbociclib (P) maintenance in patients (pts) with hormone receptor-positive (HR[+])/human epidermal growth factor receptor 2-negative (HER2[-]) advanced breast cancer (ABC): PALMIRA trial. Journal of Clinical Oncology 2023;41:1001-

Author response:

We appreciate the time and thoughtful reviews of all 3 reviewers. Ahead of a full revision of the paper, we would like to address a couple of points the reviewers have raised that we plan to address in more detail in our full revision.

(1) The relationship between membrane tension and interfacial tension: The major request by reviewers was for a better explanation of the relationship between measured mechanical parameters and membrane interfacial tension. We plan to include a schematic of the different forces at play in the membrane and to clarify our discussion and here, provide a brief explanation.

In our study, we identified a relationship between channel activation pressure and two membrane mechanical properties (area expansion modulus (K_A) and bending rigidity (K_c)) though we did not find a correlation between channel activation pressure and a third mechanical property (membrane fluidity). Through further computational analysis of the membranes, we identified an additional property called interfacial tension that helps unify and explain our results. Interfacial tension (γ) is a property akin to surface tension that reflects the chemical composition at the interface of the membrane (between the polar headgroups of the lipids and the hydrophobic acyl chains of the lipids) and balances the repulsive interaction of the nonpolar hydrocarbon chains with the polar headgroup regions of the lipids. In the established polymer brush model, the expansion modulus is proportional to the interfacial tension (W. Rawicz, Biophyiscal Journal, 2000)

γ = K_A/C,

where C is a constant. Interfacial tension occurs at the boundary between the lipid bilayer and external aqueous environment and is different from mechanical tension. While mechanical membrane tension (t) reflects a physical force in plane with the membrane, interfacial tension reflects the chemical composition at each interface of the membrane. While mechanical membrane tension depends on the size and shape of the membrane, interfacial tension is independent of these features and depends on the molecular composition of the liquid-liquid interface. An expanded discussion on this topic was recently provided (Lipowsky. Faraday Discussions. 2024). While distinct, these two properties can be related to one another via the area expansion modulus (K_A). Typically, one would imagine that upon reducing interfacial tension, and correspondingly reducing the K_A, it should now take less energy to stretch the membrane to the same extent and should reduce the activation pressure (and corresponding in plane mechanical tension ) required to open an embedded mechanosensitive channel. Interestingly though, interfacial tension also works to pull the channel open so that a reduction in interfacial tension also means more energy will be required to open the channel. We find that reductions in interfacial tension and corresponding increased energy required to open embedded channels outweighs the reduced tension that should be required to stretch the membrane. We plan to more clearly explain this tradeoff in our revision. Overal, our findings identify the exact properties driving mechanosensitive channel behavior in our study. Further, they provide a guide to understanding how and why shifts in mechanosensitive channel activation occur by connecting chemical composition changes to the changes in membrane tension propagation in a given membrane.

(2) Data presentation to support determined area expansion modulus and bending rigidity values: We will show stress strain curves used to derive Ka and kc values

(3) Address why membrane tension data was not shown for ephys experiments: The micropipette and patch clamp setups are different, and we did not use the same system for both measurements. In fact, limitations in tools that would allow for concurrent tension measurements while conducting channel activation measurements have limited our understanding of the role of membrane tension on mechanosensation to date. While recent studies have attempted to resolve this limitation through the design of new tools that enable concurrent monitoring of mechanosensitive channel activation and membrane tension (Lüchtefeld et al. Nature Methods. 2024), these tools were not available to us during our study or now. Because our study also attempted to connect these two features (membrane tension and channel activation) but we lacked tools to do so simultaneously, we used two sets of measurements to separately uncover membrane mechanical properties and channel activation pressure.

One reason it is difficult to measure membrane tension during a typical patch clamp study is because of limitations in the imaging equipment and pipettes used for this assay. The experiment is usually done by looking through the eyepiece and the pipette angle is around 45 degrees from the plane of the stage so it would be hard to visualize changes in the patch geometry in the tip of the pipette. Basically, we are able to see the pipette touch the GMPV, but cannot resolve the patch moving up the pipette. In response to the reviewer comment that tension=pressure difference times pipette radius divided by 2, we were unable to measure the radius and changes in radius of a patch upon increases in applied pressure due to the above mentioned imaging constraints. This limitation is why we were unable to directly measure applied tension with our current patch clamp set up.

(4) Interfacial tension is not experimentally measured: Interfacial tension = K_A /C where C is a constant (typically C=4 for bilayer membranes). The best way to measure interfacial tension is to determine K_A (the area expansion modulus), which we have experimentally done by generating stress vs strain curves for GPMVs. In literature, reductions in interfacial tension of a membrane are typically experimentally determined by measuring a corresponding reduction in the associated K_A value (eg. Ly and Longo. Biophys J. 2004). We have similarly followed this approach.

Author response:

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

Reviewer #1 (Public Review):

Therefore, their tool may be useful for stimulating multiple populations using a blue excitatory opsin in neuron A and their tool for red excitation of neuron B… Yet, there are no data presented that showcases their new tool for this purpose

We agree with the reviewer that in this manuscript we have not experimentally shown the applicability of our system for dual optical stimulation. However, the suppression of blue-light excitation of ZipV/T-IvfChr-expressing neurons strongly suggests this can be used in experiments exciting populations of neurons similarly shown for BiPOLES. We don’t see a theoretical basis where this experiment cannot be done if sufficient cell targeting mechanisms (such as the use of cre-lox or retroAAV) is utilized. We have started several projects pursuing these utilities in the meantime.

While they do show that red light = excitation and blue light = inhibition, they neither show 1) all-optical on/off modulation of the same cell; nor 2) high-frequency inhibition or excitation (max stim rate of 20hz, which is the same as the BiPOLES paper used for their LC stimulation paradigm; Vierock, as above, Figure 7a-d).

Regarding point 1, we understand that the reviewer asks if we have optically excited (with red light) and inhibited (with blue light) the same neurons. If so, figure 4B1 (optical excitation of ZipT-IvfCh with red light) and figure 5A (optical inhibition of  ZipT-IvfCh with blue light) represent largely the same set of neurons.

Regarding point 2, we respectfully disagree with the reviewer’s interpretation of Figure 7a-d) in Vierock et al. As we understand, in this part the authors apply a 20 Hz optical stimulation protocol to the LC neurons in vivo. However, there is no data showing that individual neurons do follow this stimulation protocol. To be clear, we are not saying that BiPOLES cannot drive 20 Hz APs. Very likely it can. It is based on ChrimsonR which is capable of doing so (Klapoetke et al., Figure 2). Although, in this manuscript we have not shown data for optical stimulation above 20Hz, our system is based on vfChrimson, which is known to drive AP of 100Hz and above (Mager et al., figure 2 and 3).  

… they must revise the manuscript to show that their approach is both 1) different in some way when compared to BiPOLES (it is my understanding that they did not do this, as per the supplementary alignment of the BiPOLES sequence and the sequence of the BiPOLES-like construct that they did test) and 2) that the properties that the investigators specifically tailored their construct to have confer some sort of experimental advantage when compared to the existing standard.

In the latest version of the manuscript, we have compared our ZipV-IvfChr and the BiPOLES construct adapted with vfChrimson (Fig. 2 Suppl 1). The mean photocurrent amplitude of IvfChr in the ZipV-IvfChr construct is ~2.7 x higher than BiPOLES adapted with vfChrimson (14 randomly selected HEK293 cells in each group) (Fig. 2 Suppl 1B). We conducted this experiment in HEK293 cells to ensure accurate voltage-clamping and less biased cell selection. Even adjusting for the smaller photocurrent of vfChrimson vs ChrimsonR, this would still translate to ~1.6 x greater photocurrent with ZipV-IvfChr compared to the original BiPOLES utilizing ChrimsonR. We believe the increased efficiency of excitation is an important aspect of adapting vfChrimson for red-light excitation of neurons.

Reviewer #2 (Public Review):

(1) In the Introduction or Discussion, the authors could better motivate the need for a red-shifted actuator that lacks blue crosstalk, by giving some specific examples of how the tool could be productively used, e.g. pairing with another blue-shifted excitatory opsin in a different population, or pairing with a GFP-based fluorescent indicator, e.g. GCaMP. The motivation for the current tool is not obvious to non-experts.

In the discussion, we now provided examples for potential use of the tool. For example, one of the key aspects that can be manipulated by the existing tool is the induction of spike-timing dependent plasticity with 2 wavelengths of light with blue light channelrhodopsin such as oChIEF is used to evoke presynaptic release and ZipT-IvfChr expressed in postsynaptic neuron. In this situation, the rapid termination of inhibitory response is critical so it does not interfere with the induction of LTP or LTD. Another experiment is the alternate control of projection neurons and interneurons in cortical areas, independent controls of neurons of direct and indirect pathways in the striatum to manipulate behavior.

(2) Simultaneous excitation and inhibition are not the same as non-excitation. The authors mentioned shunting briefly. Another possible issue is changes in osmotic balance. Activation of a Na+ channel and a Cl- channel will lead to net import of NaCl into the cell, possibly changing osmotic pressure. Please discuss.

We agree with the notion that osmotic, ionic and pH changes in small neuronal structure can be disruptive to the physiology and this is the reason we developed our approach where the fastest channelrhodopsins are used so we can minimize the channel opening time and the flux of ions through the channels when brief light illuminations are applied. Not only the flux of protons, sodium ions and calcium ions are minimized, the flux of chloride should be minimal as well (as the membrane potential should be close to the reversal potential of chloride reversal potential hence low ion flow). Hence our approach should be minimally disruptive compared to most other existing channelrhodopsin-based approaches when short or minimal light pulses were used in conjunction with our tools. This recommendation is included in the updated manuscript .

(3) The authors showed that in ZipT-IvfChr, orange light drives excitation and blue light does not. But what about simultaneous blue and orange light? Can the blue light overwhelm the effect of the orange light? Since the stated goal is to open the blue part of the spectrum for other applications, one is now worried about "negative" crosstalk. Please discuss and, ideally, characterize this phenomenon.

We now have performed this experiment. Simultaneous blue (470nm) and red light (635nm) stimulation does not produce AP (Fig .4 Suppl 1A)). This suggests the inhibitory effect of ACR is more efficient than the excitatory effects of IvfChr due to their higher conductance, this re-emphasizes the rapid termination of the ACR effects is critical for minimal disruption of physiological effects in such pairing strategy.

(3.1) Does the use of the new tool require careful balancing of the expression levels of the ZipT and the IvfChr? Does it require careful balancing of blue and orange light intensities?

As with any optogenetic tool, the users should validate the efficacy of the tool in their own system. Our tool solely relies on the balanced expression of the 2A system, the efficiency of the two opsins and their degradation of the time-span of expression. These aspects of the tool would be better addressed in future versions of the tools or improvement of the BiPOLES-type of tandem expression in subsequent versions. From the instrumentation side, the light intensity and differential penetration depth requires careful consideration. However, this holds true in most optogenetic and fluorescence imaging-based approaches as well. In the current update of the manuscript, we have included further discussion on these aspects as well.

(3.2) Also, many opsins show complex and nonlinear responses to dual-wavelength illumination, so each component should be characterized individually under simultaneous blue + orange light.

We now have performed this experiment (please see our comment to point 3)

(3.3) I was expecting to see photocurrents at different holding potentials as a function of illumination wavelength for the coexpressed construct (i.e. to see at what wavelength it switches from being excitatory to inhibitory); and also to see I-V curves of the photocurrent at blue and orange wavelengths for the co-expressed constructs (i.e. to see the reversal potential under blue excitation). Overall, the patch clamp and spectroscopic characterization of the individual constructs was stronger than that of the combined constructs.

We have added the IV curves for the co-expressed construct at different holding potentials for 470nm and 635nm wavelengths. This shows reverse potential for the two wavelengths that are intended for in vitro and in vivo applications. Performing a similar experiment for a variety of wavelengths would not be as valuable, in part, due to the enormous amount of data generated. As we have shown in the study, the response of any channelrhodopsins vary with different light duration and light intensities in addition to the wavelengths and holding potentials. The results for each recorded cell could include stimulation by different wavelengths, stimulation by different illumination intensities, stimulation with different light duration in addition to different holding potentials. Not only would the results be highly variable from cell-to-cell, there will be potentially hundreds or thousands of combinations to be tested per cell (e.g., 5 light intensities @1, 2.5 , 5 , 10 and 20 mW/mm>sup>2</sup>, 8 different wavelengths @ 450nm, 475nm, 500nm, 525nm, 550nm, 575nm, 600nm and 625nm, 7 light durations @ 1ms, 5ms, 10ms, 50ms, 100ms, 500ms and 1s, and , and 6 holding potentials @ -80mV, -70mV, -60mV, -40mV, -20mV and 0mV would result in 1680 stimulation conditions per recorded cell).Technically, the significant lowering of membrane resistance when both IvfChr and ZipACR variants are activated simultaneously would compromise the quality of voltage-clamping even in HEK293 cells with series resistance compensation. We have yet to see any other studies that had included such ambitious electrophysiology experiment for the channelrhodopsin characterization, likely due to the feasibility of such experiment.

Reviewer #3 (Public Review):

(1) The enhanced vf-Chrimson could potentially be a highlight of the manuscript, serving broader applications. Yet, gauging the overall improvements of ivf-Chrimson in comparison to other Chrimson variants remains intricate due to several reasons. First, photocurrents from ivf-Chrimson seem smaller than those from C-Chrimson (Supplemental Figure 3), and a direct comparison with standard vf-Chrimson is absent.

We appreciate the reviewer’s positive view of our modified variant. We did not emphasize this particular modification as it was identical to our previous published modification and similar to that previously published by others (CsChrimson and C1Chrimson). In all these cases, improved membrane expression was consistently detected. We believe that expression data and our comparison of C-Chrimson and IvfChr is sufficient to justify the improved membrane expression and function.

Second, while membrane expression of ivf-Chrimson appears enhanced in provided brightfield recordings, the quantitative analysis would necessitate confocal microscopy and a membrane marker (Supplemental Figure)

We have now quantified the results with a membrane palmitoylated mCherry using confocal microscopy shown in Fig 2 Suppl1 A. We measured the Pearson Correlation Coefficient of the mCherry with EGFP or Citrine signal for the 6 constructs (vfChrimson, vfChrimson with trafficking sequence, vfChrimson with N-terminal signaling peptide from oChIEF (C-vfChrimson), vfChrimson with trafficking sequence and N-terminal signaling peptide from oChIEF (IvfChr), BiPOLES with EGFP or citrine and vfChrimson) and the results were identical and consistent with the prior results using epifluorescence microscopy.

(2) Finally, other N-terminal modified Chrimson variants, like CsChrimson by Klapoetke et al. in 2014 and C1Chrimson by Oda et al. in 2018, have been generated. Comparing ivf-Chrimson to vf-CsChrimson or vf-C1Chrimson would be important to evaluate the benefits of the applied N-terminal modification.

Our development of IvfChrimson is similar to the approach of vf-CsChrimson and identical to that of vf-C1Chrimson and we do not claim these modifications to be unique or superior. However, we have developed our design independently of these other studies and we have more extensive functional comparison and characterization data of our IvfChrimson variant than the other studies.

(2.1) The action spectra of ZipACR suggest peak absorption of ZipACR WT and its mutant at 525 - 550 nm (Fig. 3). This is even further red-shifted than previously reported by Govorunova et al. Further action spectra recordings differ for all constructs between recordings initiated with blue or red light (Supplementary Fig. 5). This discrepancy is unexpected and should be discussed.

We thank the reviewer for the comment, this was a mistake in the traces used for the figure. The example traces were the spectral response measured from the 400 nm to 650 nm instead of the 650 nm to 400 nm order shown in the spectral data. This has now been corrected.

Additionally, the representative photocurrents of Zip(151V) in Fig. 3D1 do not align with the corresponding action spectrum in Fig. 3D2 as they show maximal photocurrents for 400 nm excitation.

Please, see point above.

(3) The authors introduce two different bicistronic expression cassettes-ZipT-IvfChR and ZipV-IvfChR-without providing clear guidelines on their conditions of use. Although the authors assert that ZipT is slower and further red-shifted than ZipV, the differences in the data for both ACR mutants are small and the benefits of the different final constructs should be explained.

In our testing in neurons, ZipT has less ‘escaped’ spikes after the termination of the light pulses in the cells we have tested. However, this is dependent on the membrane properties such as capacitance and resistance of the cells. ZipV has a faster termination time and in some situations may be necessary due to its faster termination time and reduced disruption of physiological processes.

We have now included this discussion in our updated manuscript.

(4) The ZipT/V-IvfChRs are designed as bicistronic constructs; yet, disparities in membrane trafficking and protein degradation between the two channels could lead to divergences in blue and red light photoresponses. For future applicants, understanding the extent of expression ratio variations across cells using the presented expression cassettes could be of significance and should be discussed.

We now have included this discussion in our responses above.

Reviewer #1 (Recommendations For The Authors):

(1) The Figure 1a mV cartoon traces for chloride are confusing. The chloride currents are depolarizing, not hyperpolarizing. As noted by the authors, these channels largely generate AP blockade through shunting inhibition (division), not hyperpolarization (subtraction).

The figure has been corrected.

(2) Figure 2A does not show where the light is applied. Why are some of the bars blue and some of them not filled?

This has been corrected

(3) Figure 2C1 does not show where the light is applied. There should be an inset to detail the blue-light-cessation-evoked AP. Also doesn't give the holding potential.

The requested details are added.

(4) Figure 2C2 inset is described as showing that "Light-induced currents with 470 nm illumination were initially outward but turned inward immediately following light offset." Is that correct? It looks to me like the current turns inward about half-way through the light pulse and then becomes even stronger after the light turns off. That is also consistent with the CC traces, which appear to show a transition toward depolarization during the light pulse before the AP initiation at light offset.

Yes, the reviewer's observation is correct. There are blue light-induced outward and inward current peaks at the onset and offset of the light. Accordingly, we have modified the phrasing for Fig. 2C2.

(5) Figure 3D1 shows that Zip(151V) has a peak current at 400nm, with a steady increase in current from red to blue, however, this is not the case in the summary data in 3D2. It's also not shown in Supplementary Figure 5B. What's going on?

We apologize for the prior version of the figure associated with the first submission. The example traces from 400nm -> 650 nm were incorrectly included in the figure whereas the 650nm -> 400 nm example traces should be included. This has been corrected.

(6) Figure 3D1 has no time scale.

It is now been included

(7) Figure 3E1 should read "Transduced" and not "Transfected"

This has been corrected.

(8) IvfChr fidelity drops off dramatically at 20hz...down to 50% efficiency of generating APs. This is described in the legend as "high frequency". Maybe the cart came before the horse in this figure...as it looks like in panel C that using less light power density improves fidelity in the dual opsin configuration with red light stimulation...why not use that power for the characterization? Did you try any higher frequencies? Or longer pulse widths? This is an important characterization to inform further use of the tool. This shortcoming isn't a cell-intrinsic limitation, as the 470nm stim with IVfChr was 100% successful at both 10hz and 20hz.

It is known that red but not blue light pulses induce desensitization (optical fatigue) in red-shifted ChR variants. Indeed, one can reinstate the response to red light, by giving violet-blue light pulses (Fig 4. Suppl 2). We think this is the reason that the 470nm stimulation was more effective in inducing AP in cells expressing IvfChR. Higher light intensities induce greater desensitization, but are preferred for faster opening of channels and depolarization of neurons. This can explain why, in some situations, lower light intensities were more effective in producing APs when pulse trains were used. We have recordings from cells firing APs at 40Hz (not included). All these cells had high expression levels of the opsin.   

(9) Figure 4D: why use 100ms pulse width? How do you know that this isn't causing depol block? Or some of the nefarious concerns that are raised in the discussion, such as "...disrupt[ion of] normal neuronal physiology and signal processing that occurs in millisecond time scale"?

We used 100ms pulse duration to follow the published protocol that this experiment is based on (Lin et al., 2013, Nature Neuroscience). 

(10) Figure 4E-bottom: What is the blue peak at light onset? Is the tool driving early activation before silencing?

There seems to be an early, sharp and brief activation by blue light. We don’t know the definite cause of this, but we speculate this is driven by blue-light activation of ZipACR and not the IvfChr portion of the construct. The reason is that such a sharp rise is absent when only IvfChr is expressed (Fig. 4E, upper panel). Soma-targeted motif tethered to channelrhodopsins is known to result in preferential expression of channels close to soma but does not exclude the expression of channelrhodopsin in axonal and dendritic compartments, especially when animals are allow to recover for long period of time after viral injection. We believe that ZipACR at axonal terminals where the chloride concentration is high can still cause blue-light evoked depolarization and transmitter release. We observed this phenomenon in two mice in their first trial. The data for individual trials for each mouse are included in a supplementary table.

(11) Figure 4G: Earlier in this same figure (B2, C), 470nm light was more effective at stimulating IvfChr than 635nm light. Is it unexpected that 638nm light would in this in vivo context be more effective at driving IvfChr responses than 450 nm light (at least as reflected by the AUC measurements)? Does this reflect fiber placement and light penetration/scattering?

The spectral peaks of Chrimson-based variants including vfChrimson are all centered around 600 nm, and at 635 / 638 nm light, the amplitudes of photo-response decline, the channel onset slows, and the channels suffer greater desensitization. In isolated preparations where the light penetration is similar between 635 / 638 nm and 470 nm, 470 nm responses can outperform 635 / 638 nm responses due to its lack of desensitization and higher consistency in its response. This is also a strong reason that we have developed our current approach. In in vivo preparation shown in Fig. 4D-G, the much higher tissue penetration of 638nm light due to reduced absorption and reduced scattering can offset the performance of IvfChr to 450 nm light.  

(12) In the methods, it is noted that different viral batches appear to generate different levels of neuronal toxicity. If that is the case, how did you differentiate between true differences between constructs vs. differential cell health effects?

For figure 4D-F (whisker movement), we determined virus toxicity using NeuN staining. In slice recordings, we used the electrophysiological property of the neurons to assess their health. For this manuscript, we had one batch of virus that produced toxicity. We did not include any data from this batch.

Reviewer #2 (Recommendations For The Authors):

● Define AUC on first use.

It is now defined.

● Figure 3C2: Please explain how the photocurrents were normalized. As presented, it looks like under strong orange light, the ZipACR has higher photocurrent than the ivfChr.

This is due to the fact vfChrimson and other Chrimson-based variants do not fully recover in the dark after 590 nm stimulation. We tested IvfChrimson with both reconditioning light pulse of 405 nm and without 405 nm and we can consistently reach a greater ‘maximal’ response from the same cell after 405 nm reconditioning (see Fig. 4 Suppl 2). We therefore normalize the response to the maximal recorded response of the cell often achieved with 10 or 20 mW/mm² 590 nm stimulation after 405 nm reconditioning. We understand this can be confusing and have now replaced the light-intensity response in Fig. 3C2 with the one with 405 nm reconditioning which is easier to interpret for the readers.

● P. 3: "As expected, blue light pulses induce transient membrane suppression..." Unclear what "suppression" means. Shunting? Hyperpolarization?

We rephrased this to “As expected, blue light pulses transiently suppress APs…”

● P. 3: "illumination at 470 nm and 590 nm wavelengths led to similar amounts of courtship song (110.1 {plus minus} 12.8 and 78.5 {plus minus} 11.6,n = 16-17, respectively)". What are the units of "courtship song"?

The unit for courtship song is the number of pulses per 10 seconds. This has been clarified in the figure.

● P. 5: The quantification of photocurrent in terms of pA/pF/A.U. is non-standard. I understand the impetus to normalize by expression to give something proportional to per-molecule conductance, but a user cares about overall photocurrent. Please also give the real photocurrents, either pA or pA/pF.

We have provided the real photocurrent in pA or pA/pF where scientifically appropriate. To avoid selection and experimenter’s bias in our data, we did not set criteria for data elimination for cells with specific fluorescence intensity or photocurrent amplitude. Some resulting response can range from vary up to 20 folds from the same construct in many experiments. We do not believe that averaging absolute photocurrent amplitude would be justified due to the imbalance of weighing in the results. We do acknowledge that not selecting or eliminating data points would introduce higher noise in recordings with smaller responses but this is preferable over the selection or experimenter bias that is likely to be introduced otherwise.

● Please quote illumination intensities wherever possible.

● P. 7: why was the red light crosstalk into Zip(151T) tested at 635 nm instead of 590 nm? Isn't the relevant parameter 590 nm, since that will be used for the excitatory opsin?

In all our characterizations of the constructs using slice electrophysiology recordings, we used 635nm instead of 590nm. The reason is that compared to 590nm wavelength, at 635nm the photocurrent for Zip(151T) and Zip(151V) is significantly reduced (Fig. 3D1,D2).

● P. 10: "we examined the power at which responses to 470 nm and 635 nm lights induce APs in neurons expressing ZipT-IvfChr, ZipV-IvfChr, or IvfChr", but the preceding sentence says you didn't test the ZipT-IvfChr. This is confusing, please clarify.

The previous paragraph refers to the photocurrent recordings in HEK293 cells where our fast LED based illumination system is limited to 590 nm light, whereas the subsequent paragraph refers to the brain slice neuronal recordings. We have now emphasized the difference of the experiments in the rewrite.

● Fig. 4B1, top: Why don't the blue traces return to the same baseline after the stimulus epochs?

We observed this shift in baseline (~4mV more depolarized) in cells expressing IvfChR (or vfChR) only with blue light stimulation. This was observed in the neurons recorded in the CA1 as well (data not shown). There was no such a change following red light stimulation (Fig. 4B1). Therefore, this should not affect the applicability of our construct. The original paper introducing vfChR did not test the responses of their constructs to blue light. There could be another photocycle state that is activated stronger by 470nm than 590nm and it has a slow off-rate, but this is only a speculation from our side. It must be noted we did not observe such a phenomenon in cells expressing ChrimsonR (Fig. 1 Suppl 1C).

● Fig. S3B, right: The two colors are barely distinguishable on the graph. Consider more distinct colors and/or different symbols.

It has been changed accordingly.

● P. 15: "However, we do not recommend the use of orange light pulses, as we observed a significant photocurrent in this wavelength." Not clear what this is referring to. Which construct? Under which circumstances shouldn't one use orange light pulses? Where's the data showing this?

This is referring to Fig. 3D1,D2 and Figure 4 suppl Fig. 2 which show a normalized ~40-50% photocurrent at 590nm. Now in the text, the reference figures for the data are added.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

Audio et al. measured cerebral blood volume (CBV) across cortical areas and layers using high-resolution MRI with contrast agents in non-human primates. While the non-invasive CBV MRI methodology is often used to enhance fMRI sensitivity in NHPs, its application for baseline CBV measurement is rare due to the complexities of susceptibility contrast mechanisms. The authors determined the number of large vessels and the areal and laminar variations of CBV in NHP and compared those with various other metrics.

Strengths:

Non-invasive mapping of relative cerebral blood volume is novel for non-human primates. A key finding was the observation of variations in CBV across regions; primary sensory cortices had high CBV, whereas other higher areas had low CBV. The measured CBV values correlated with previously reported neuronal and receptor densities.

Weaknesses:

A weakness of this manuscript is that the quantification of CBV with postprocessing approaches to remove susceptibility effects from pial and penetrating vessels, as well as orientation dependency, is not fully validated, especially on a laminar scale. Further specific comments follow.

We suspect that the comment regarding the lack of validation on laminar level stems from an error made by the corresponding author in the original bioRxiv submission (v1, May 17th https://www.biorxiv.org/content/10.1101/2024.05.16.594068v1?versioned=true), where Figure 3 which contains laminar validation was lost during pdf conversion. After submitting to E-Life, this mistake was quickly identified, and a corrected manuscript was re-uploaded to the bioRxiv (v2, June 5th, https://doi.org/10.1101/2024.05.16.594068). Although we informed the eLife staff about the update, it appears that the revised manuscript may not have reached reviewer #1 in time. We sincerely apologize for any confusion or inconvenience this may have caused.

(1) Baseline CBV indices were determined using contrast agent-enhanced MRI (deltaR2*). Although this approach is suitable for areal comparisons, its application on a laminar scale has not been validated in the literature or in this study. By comparing with histological vascular information of V1, the authors attempted to validate their approach. However, the generalization of their method is questionable. The main issue is whether the large vessel contribution is minimized by processing approaches properly in various cortical areas (such as clusters 1-3 in Figure 5). It would be beneficial to compare deltaR2* with deltaR2 induced by contrast agents in a few selected slices, as deltaR2 is supposed to be sensitive to microvessels, not macrovessels. Please discuss this issue.

The requested validation is presented in Figure 3F, which compares our deltaR2* measurements with previously invasive estimates of large vessel, capillary and cytochrome oxidase (CO) levels in V1 (Weber et al., 2008; doi.org/10.1093/cercor/bhm259). Our deltaR2* values show a stronger correspondence with microvascularity and CO levels than large vessels. Moreover, Figure 3D illustrates relative differences between V1 and V2, which closely align with the relative vascular volume differences reported by Zheng et al., 1991. It is important to note that Weber and colleagues averaged across V2-V5 due to similar vascularity across these areas. In our material, we also observed similar vascularity in these areas, though V5 (e.g., MT) has slightly denser vascularity, in agreement with reports of CO staining.

Additionally, we report similar GM/WM vascular density, and high vascular density in primary sensory areas. Unfortunately, available ground-truth data on vascularity does not provide further (general) validation data for laminar vasculature in macaques (such as those in cluster 1-3; Fig. 5). That said, we have provided substantial evidence linking whole-brain vascular measures with variations in neuron (for data distribution, see Supp. Fig. 6F) and receptor densities, which we believe provides strong support for our approach.

We would like to clarify that the authors do not assert that gradient-echo MRI is exclusively sensitive to microvessels and not macrovessels. This is not stated anywhere in the manuscript. If any sentence appears misleading, please let us know, and we will consider revising it. It is well-established that large vessels contribute to ΔR2* (Ogawa et al., 1993; Boxerman et al., 1995), and this is clearly stated in the manuscript (introduction, methods, results and discussion) and demonstrated in Figures 2A, B, and Supp. Figs. 2, 3, and 4. The primary concern, as the reviewer also noted, is whether we have sufficiently minimized the contribution of large vessels in our parcellated data analysis.

At the parcellated level, we used the median value to avoid skewness in the data distribution, which primarily arises from large vessels, as regions near these vessels exhibit higher ΔR2*. The skewness of ΔR2* is also visible in Figure 1F, G. While this approach mitigates this large-small vessel issue, it does not entirely resolve it, as a slight linear increase toward the cortical surface remains (in all parcels). This is likely due to our inability to delineate all penetrating vessels as shown in Figure 2E and because contrast agents cumulatively accumulate toward superficial layers where blood originates and returns to the pial surface. To mitigate this issue, we detrended across layers the parcellated profiles, obtaining results similar to the ground-truth measures of vascularity in V1-V5 and CO histology in V1.

(2) High-resolution MRI with a critical sampling frequency estimated from previous studies (Weber 2008, Zheng 1991) was performed to separate penetrating vessels, which is considered one of the major advancements in this study. However, this approach is still insufficient to accurately identify the number of vessels due to the blooming effects of susceptibility and insufficient spatial resolution. There was no detailed description of the detection criteria. More importantly, the number of observable penetrating vessels is dependent on imaging parameters and the dose of the contrast agent. If imaging slices were obtained in parallel to the cortex with higher in-plane resolution, it would likely improve the detection of penetrating vessels. Using higher-field MRI would further enhance the detection of penetrating vessels. Therefore, the reported value is only applicable to the experimental and processing conditions used in this study. Detailed selection criteria should be mentioned, and all potential pitfalls should be discussed.

We believe that Figure 2 represents a significant conceptual and data analysis advancement in the field of vascular imaging. To the best of our knowledge, this is the first MRI study attempting to assess vessel density across cortical layers and compare the number of vessels to the known ground-truth. While we do not claim to have achieved a perfect solution (as shown in Figure 2), we offer a robust challenge to the imaging community by introducing this novel benchmarking approach. Our hope is that this conceptual framework will inspire the MR imaging community to tackle this challenge.

Regarding imaging parameters, TE did not have much effect on our results, with a slight effect observed in the superficial layers due to the presence of large pial vessels (blooming effect; Fig. 2C). This also suggests that similar results could be achieved by changing the contrast agent dose, though there are, of course, CNR requirements and limitations at either end of the spectrum.

We completely agree with the reviewer that spatial resolution is critical in resolving the arterio-venous networks, and we have dedicated significant attention to this topic in the introduction, results and discussion sections. We also agree with the reviewer that if imaging slices were obtained in parallel to the cortex with higher in-plane resolution, it would improve the detection of vessels. However, while this approach is ideal for counting vessels in a single plane and isolated region of cortex, it is less suited to the surface mapping of vessels, which is the focus of our study.

Regarding the exclusion of vessels, based on visual comparison of vessels in volume space, Frangi-filter detection of vessels in volume space, and surface detection of vessels, we found no evidence to develop additional exclusion criteria (Supp. Fig. 3). On the contrary, we identified a number of false negatives in both the surface maps and volume maps. Notable exceptions to this rule seemed to occur at premotor areas F2 and F3 (Matelli et al., 1984; Patterns of cytochrome oxidase activity in the frontal agranular cortex of the macaque monkey). In these regions, we observed peculiar “pockets” of signal drop-out in equivolumetric layers 4-5. It is unclear what these signal-voids represent but it is interesting to note that these cortical areas F1-F5 were originally delineated by distinct CO+ positive large cells (Matelli et al., 1984).

(3) Attempts to obtain pial vascular structures were made (Figure 2). As mentioned in this manuscript, the blooming effect of susceptibility contrasts is problematic. In the MRI community, T1-based Gd contrast agents have been used for mapping large vasculature, which is a better approach for obtaining pial vascular structures. Alternatively, computer tomography with a blood contrast agent can be used for mapping blood vasculature noninvasively. This issue should be discussed.

We agree with the reviewer that T1-based contrast agents may offer more precise direct localization of large vessels in pial vasculature. However, the primary focus of our study was not on visualizing pial vascular structures, but rather on measuring vascular volume across cortical layers. For this purpose, we opted to use ferumoxytol, which provides superior T2*-contrast and about ten times longer plasma half-life compared to gadolinium. While we anticipated artifacts from the pial network, we developed a novel method to indirectly map these long-distance susceptibility artifacts arising from large vessels onto the cortical surface (Fig. 2A). If the goal would be to specifically visualize pial vessels, we applaud the high-resolution TOF angiography developed for direct vessel visualization (Bollman et al., 2022; https://doi.org/10.7554/eLife.71186)

Changes in text:

“4.1 Methodological considerations - vessel density informed MRI

While the pial vessels can be directly visualized using high-resolution time-of-flight MRI (Bollmann et al., 2022), and computed tomography (Starosolski et al., 2015), imaging of the dense vascularity within the large and highly convoluted primate gray matter presents other formidable challenges. Here, we used a combination of ferumoxytol contrast agent and cortical layer resolution 3D gradient-echo MRI to map cerebrovascular architecture in macaque monkeys. These methods allowed us to indirectly delineate large vessels and indirectly estimate translaminar variations in cortical microvasculature.”

(4) Since baseline R2* is related to baseline R2, vascular volume, iron content, and susceptibility gradients, it is difficult to correlate it with physiological parameters. Baseline R2* is also sensitive to imaging parameters; higher spatial resolution tends to result in lower R2* values (closer to the R2 value). Therefore, baseline R2* findings need to be emphasized.

We agree with the reviewer's comment on the complexity of correlating baseline R2* with vasculature, given its sensitivity to multiple factors such as venous oxygenation, iron content, and imaging parameters such as image resolution. While our study focuses on vascular measurements, one could also highlight iron’s role in brain energy metabolism. Deoxygenated blood affects R2*, iron in oligodendrocytes supports myelination and neuronal signaling, and iron’s role in cytochrome c oxidase during electron transport impacts mitochondrial energy production. These metabolic factors collectively affect baseline R2* and link it to vasculature. Though quantitative susceptibility mapping (QSM) could help differentiate these different factors, it is beyond the scope of this study.

(5) CBV-weighted deltaR2* is correlated with various other metrics (cytoarchitectural parcellation, myelin/receptor density, cortical thickness, CO, cell-type specificity, etc.). While testing the correlation between deltaR2* and these other metrics may be acceptable as an exploratory analysis, it is challenging for readers to discern a causal relationship between them. A critical question is whether CBV-weighted deltaR2* can provide insights into other metrics in diseased or abnormal brain states. If this is the case, then high-resolution deltaR2* will be useful. Please comment on this possibility.

We agree with the reviewer that correlation deltaR2* with other metrics, such as myelin and cortical thickness, receptors and interneuron types, remains exploratory. Establishing causal relationships requires advanced multivariate analysis across cortical layers, but mapping histological stains to cortical layers is still under development. While this exploratory approach is promising, the ability to apply these insights to diseased or abnormal brain states is not yet clear. Layer-specific analysis of vasculature and function in disease is a future goal, and ongoing work aims to expand this line of inquiry. For now, while high-resolution deltaR2* may indeed offer diagnostic potential, we prefer to refrain from overstating its clinical utility at this stage. We agree that multimodal studies integrating neuroanatomy, function, and vascular metrics will be valuable for deeper insights into brain abnormalities.

Changes in text:

“4.3 The vascular network architecture is intricately connected to the neuroanatomical organization within cerebral cortex

…To comprehensively understand the factors contributing to the vascular organization of the brain, experimental disentanglement through multivariate analysis of laminar cell types and receptor densities is needed (Hayashi et al., 2021, Froudist-Walsh et al., 2023).”

(6) There is no discussion about the deltaR2* difference across subcortical areas (Figure 1). This finding is intriguing and warrants a thorough discussion in the context of the cortical findings.

We thank the reviewer for this comment. We have expanded discussion on subcortical structures:

Section 4.3, 1st paragraph:

“In the cerebral cortex, neurons account for a significant portion (≈80-90%) of energy demand, with most of this energy allocated to signaling (≈80%) and maintaining membrane resting potentials (≈20%) (Attwell and Laughlin, 2001; Howarth et al., 2012). Since firing frequency is modulatory and the neural networks utilize distributed coding, the maintenance of resting-state membrane potential determines the minimal energy budget and the lower-limit for cerebral perfusion. Based on neuronal variability and energy dedicated to maintaining surface potential, this suggest an approximate (4 × 20% ≈) 80% variation in CBF and a resultant 25% variation in CBV across the cortex, in line with Grubbs' law (CBV = 0.80 × CBF0.38) (Grubb et al., 1974). In the cerebellar cortex, neuron density is higher, and the resting potentials are thought to account for more than 50% of energy usage (Howarth et al., 2012), aligning with its higher vascular volume compared to the cerebral cortex (Fig. 1F). However, this is a simplified estimation, and a more comprehensive assessment would need to account for consider an aggregate of biophysical factors such as…”

Section 4.3, 4th paragraph:

“When viewed in terms of information flow, CBV appear to decrease along the canonical circuit pathway (e.g., L4→L2/3→L5) in the primary visual cortex (Douglas and Martin, 2007) and as one ascends the hierarchy (e.g., V1→V2→V3&4→MT→7A) from primary sensory areas (Fig. 3F, Supp. Fig. 8) (Felleman and Van Essen et al., 1991, Markov et al., 2014). A similar pattern is observed in the auditory hierarchy, where the inferior colliculus, an early processing hub, exhibits the highest vascular volume, followed by a gradual reduction along cortical auditory ‘where’ and ‘what’ pathways (Fig. 1F, Fig. 3B).”

(7) Figure 3 is missing. Several statements in the manuscript require statistics (e.g., bimodality in Figure 2D, Figure 3F).

We apologize to the reviewer for the absence of Figure 3 in the initial submission.

As for statistical testing of bimodality, we respectfully disagree and feel that this would not add much value to the manuscript. We think a descriptive, rather than rigorous, approach is sufficient in this context.

Reviewer #2 (Public review):

Summary:

This manuscript presents a new approach for non-invasive, MRI-based measurements of cerebral blood volume (CBV). Here, the authors use ferumoxytol, a high-contrast agent, and apply specific sequences to infer CBV. The authors then move to statistically compare measured regional CBV with the known distribution of different types of neurons, markers of metabolic load, and others. While the presented methodology captures an estimated 30% of the vasculature, the authors corroborated previous findings regarding the lack of vascular compartmentalization around functional neuronal units in the primary visual cortex.

Strengths:

Non-invasive methodology geared to map vascular properties in vivo.

Implementation of a highly sensitive approach for measuring blood volume.

Ability to map vascular structural and functional vascular metrics to other types of published data.

Weaknesses:

The key issue here is the underlying assumption about the appropriate spatial sampling frequency needed to capture the architecture of the brain vasculature. Namely, ~7 penetrating vessels / mm2 as derived from Weber et al 2008 (Cer Cor). The cited work begins by characterizing the spacing of penetrating arteries and ascending veins using a vascular cast of 7 monkeys (Macaca mulatta, same as in the current paper). The ~7 penetrating vessels / mm2 are computed by dividing the total number of identified vessels by the area imaged. The problem here is that all measurements were made in a "non-volumetric" manner and only in V1. Extrapolating from here to the entire brain seems like an over-assumption, particularly given the region-dependent heterogeneity that the current paper reports.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

- For broader readership, it would be beneficial to provide a guide on how to interpret baseline R2* versus ΔR2*.

The text was edited as follows:

“…For quantitative assessment, R₂* values were estimated from multi-echo gradient-echo images acquired both before and after the administration of ferumoxytol contrast agent (Table 1). Subsequently, the baseline R₂* and ΔR₂*, an indirect proxy measure of CBV (Boxerman et al., 1995), volume maps for each subject were mapped onto the twelve native equivolumetric layers (ELs) (Fig. 1C). Each vertex was then corrected for normal of the cortex relative to B₀ direction (Supp. Fig. 1). Surface maps for each subject were registered onto a Mac25Rhesus average surface using cortical curvature landmarks and then averaged across the subjects (Fig. 1D, E). Around cortical midthickness, the distribution of R₂*, an aggregate measure for ferritin-bound iron, myelin content and venous oxygenation levels (Langkammer et al., 2012), resembled the spatial pattern of ΔR₂* vascular volume. However, across cortical layers, these measures exhibited reversed patterns: R₂* increased toward the white matter surface, whereas ΔR₂ decreased (Fig. 1E, G).”

- The legends in Figure 1 describe green/cyan arrows, which are not visible in the figure itself.

We thank the reviewer for noting this discrepancy. The reference to green/cyan arrows was removed from the Figure 1 legend.

- There are typos in Section 3.3: "(Figure 4A, E)" and "(cluster 3; Figure 3)" should be corrected to Figure 5.

We thank the reviewer for noting this error. The references to the Figures were corrected.

Reviewer #2 (Recommendations for the authors):

The work is elegantly presented and very easy to follow. The figures and the data presented there are compelling and well-organized. I have enjoyed reading the paper, despite my disagreement with the validity of the methodology presented.

Validation against MRA methods (high resolution needed here, Bolan et al 2006, cited also by the authors). Certainly, that work used a much higher magnetic field. This could be done through collaboration if such a magnet is not available. In my humble opinion, the current arguments provided in the paper as validation fall short in convincing future readers. Other TOF approaches might be better suited (in combination with line scanning or single plane sequences) for the 3T used in this work.

We appreciate the reviewer’s suggestion regarding time-of-flight (TOF) angiography at ultra-high magnetic fields, such as 9.4T for improved visualization of fast-flowing blood in arterial vessels, as elegantly demonstrated in Bolan et al., 2006. However, our focus was on mapping vasculature across cortical layers and TOF is not optimal for imaging slow capillary blood inflow. To enhance CNR also at capillary level, we used ferumoxytol-contrast agent to create quantitative CBV-weighted cortical layer maps (Boxerman et al., 1995).

We are open to collaborative opportunities to revisit this work using ultra-high magnetic field strengths and more detailed neuroanatomical ground-truth measures. However, the recommended line scanning or single-plane sequences, at least on first impression, seem inadequate for whole-brain coverage and cortical surface mapping.

Some of the methodology can be made more accessible to non-MRI readers. For example, a more elaborate explanation of R2* and ΔR2 could benefit future readers.

Elaborated as requested (see above reply).

A more detailed discussion of the limitations of the methodology could also be beneficial here. Explain the potential implications of under-sampling denser vascular areas (i.e. with potentially more than 7 penetrating vessels per mm2).

V1, with its highest neuronal density, likely also has the highest feeding/draining vessel density. Based on this, we hypothesized that a 0.23 mm isotropic image resolution would sufficiently capture cortical arterio-venous networks, but we did not achieve the expected detection of 7 penetrating vessels per mm². Consequently, we refrained from quantifying vessel density in other areas, albeit we did report the total vessel count.

This under-sampling likely biases our ΔR2* estimates, skewing them toward larger vessels. To address this, we used median parcel values to avoid over-representing large vessels (the long-tail in ΔR2 parcels data distribution represents large vessels) and corrected for the cortical surface bias where blood originates from and returns to the pial network. These steps helped mitigate large vessel bias as described in the methods, results and discussion (see also our response to Reviewer #1, question #1).

To improve clarity for readers, we further clarified:

Methods:

“The effect of blood accumulation in large feeding arteries and draining veins toward in the superficial layers was estimated using linear model and regressed out from the parcellated ΔR₂* maps.”

Results:

“To mitigate bias resulting from undersampling the large-caliber vessels (Fig. 2A, B), median parcel values were obtained and M132 parcellated ΔR2* profiles were then detrended across ELs in each subject and then averaged.”

Discussion:

“This methodology, however, has known limitations. First, gradient-echo imaging is more sensitized toward large pial vessels running along the cortical surface and large penetrating vessels, which could differentially bias the estimation of Δ R₂* across cortical layers (Fig. 2A, 2B) (Boxermann et al., 1995; Zhao et al., 2006). Additionally, vessel orientation relative to the B₀ direction introduce strong layer-specific biases in quantitative ΔR₂* measurements (Supp. Fig. 1C) (Ogawa et al., 1993; Viessmann et al., 2019; Lauwers et al., 2008). To address these concerns, we conducted necessary corrections for B₀-orientation, obtained parcel median values and regressed linear-trend thereby mitigating the effect of undersampling large-caliber vessels across ELs (Fig. 2C, Supp. Fig. 1).” 

Please note, we are currently unable to create BALSA links to the figures due to maintenance issues at the data repository. As a result, we have opted to remove the links:

Author response:

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

Reviewer #1:

(1) You claim transdiagnostic phenotypes are temporally stable -- since they're relatively new constructs, do we know how stable? In what order?  

This is an important question. We have added two recent references to support this claim on page 1 and cite these studies in the references on pages 25 and 28:

“Using factor analysis, temporally stable (see Fox et al., 2023a; Sookud, Martin, Gillan, & Wise, 2024), transdiagnostic phenotypes can be extracted from extensive symptom datasets (Wise, Robinson, & Gillan, 2023).”

Fox, C. A., McDonogh, A., Donegan, K. R., Teckentrup, V., Crossen, R. J., Hanlon, A. K., … Gillan, C. M. (2024). Reliable, rapid, and remote measurement of metacognitive bias. Scientific Reports, 14(1), 14941. https://doi.org/10.1038/s41598-024-64900-0

Sookud, S., Martin, I., Gillan, C., & Wise, T. (2024, September 5). Impaired goal-directed planning in transdiagnostic compulsivity is explained by uncertainty about learned task structure. https://doi.org/10.31234/osf.io/zp6vk

More specifically, Sookud and colleagues found the intraclass correlation coefficient (ICC) for both factors to be high after a 3- or 12 month period (ICC_{AD_3} = 0.87; ICC_{AD_12} = 0.87; ICC_{CIT_3} = 0.81; ICC_{CIT_3}= 0.76; see Tables S41 and S50 in Sookud et al., 2024).

(2) On hypotheses of the study: 

I didn't understand the logic behind the hypothesis relating TDx Compulsivity -> Metacognition > Reminder-setting

It seems that (a) Compulsivity relates to overconfidence which should predict less remindersetting

Compulsivity has an impaired link between metacognition and action, breaking the B->C link in the mediation described above in (a). What would this then imply about how Compulsivity is related to reminder-setting?

"In the context of our study, a Metacognitive Control Mechanism would be reflected in a disrupted relationship between confidence levels and their tendency to set reminders."  What exactly does this predict - a lack of a correlation between confidence and remindersetting, specifically in high-compulsive subjects?

Lastly, there could be a direct link between compulsivity and reminder-usage, independent of any metacognitive influence. We refer to this as the Direct Mechanism  Why though theoretically would this be the case? 

"We initially hypothesised to find support for the Metacognitive Control Mechanism and that highly compulsive individuals would offload more". 

The latter part here, "highly compulsive individuals would offload more" is I think the exact opposite prediction of the Metacognitive control mechanism hypothesis (compulsive individuals offload less). How could you possibly have tried to find support, then, for both? 

Is the hypothesis that compulsivity positively predicts reminder setting the "direct mechanism" - if so, please clarify that, and if not, it should be added as a distinct mechanism, and additionally, the direct mechanism should be specified. 

There's more delineation of specific hypotheses (8 with caveats) in Methods. 

"We furthermore also tested this hypothesis but predicted raw confidence (percentage of circles participants predicted they would remember; H6b and H8b respectively)," What is the reference of "this hypothesis" given that right before this sentence two hypotheses are mentioned?  To keep this all organized, it would be good to simply have a table with hypotheses listed clearly. 

We agree with the reviewer that there is room to improve the clarity of how our hypotheses are presented. The confusion likely arises from the fact that, since we first planned and preregistered our study, several new pieces of work have emerged, which might have led us to question some of our initial hypotheses. We have taken great care to present the hypotheses as they were preregistered, while also considering the current state of the literature and organizing them in a logical flow to make them more digestible for the reader. We have clarified this point on page 4:

“Back when we preregistered our hypotheses only a limited number of studies about confidence and transdiagnostic CIT were available. This resulted in us hypothesising to find support for the Metacognitive Control Mechanism and that highly compulsive individuals would offload more due to an increased need for checkpoints.”

The biggest improvement we believe comes from our new Table 1, which we have included in the Methods section in response to the reviewer’s suggestion (pp. 21-22):

“We preregistered 8 hypotheses (see Table 1), half of which were sanity checks (H1-H4) aimed to establish whether our task would generally lead to the same patterns as previous studies using a similar task (as reviewed in Gilbert et al., 2023).”

We furthermore foreshadowed more explicitly how we would test the Metacognitive Control Mechanism in the Introduction section on page 4, as requested by the reviewer:

“In the context of our study, a Metacognitive Control Mechanism would be reflected in a disrupted relationship between confidence levels and their tendency to set reminders (i.e., the interaction between the bias to be over- or underconfident and transdiagnostic CIT in a regression model predicting a bias to set reminders).”

To avoid any confusion regarding the term ‘direct’ in the ‘Direct Mechanism’, we now explicitly clarify on page 4 that it refers to any non-metacognitive influences. Additionally, we had already emphasized in the Discussion section the need for future studies to specify these influences more directly.

Page 4: “We refer to this as the Direct Mechanism and it constitutes any possible influences that affect reminder setting in highly-compulsive CIT participants outside of metacognitive mechanisms, such as perfectionism and the wish to control the task without external aids.”

The reviewer was correct in pointing out that, in the Methods section, we incorrectly referred to ‘this hypothesis’ when we actually meant both of the previously mentioned hypotheses. We have corrected this on page 23:

“We furthermore also tested these hypotheses but predicted raw confidence (percentage of circles participants predicted they would remember; H6b and H8b respectively), as well as extending the main model with the scores from the cognitive ability test (ICAR5) as an additional covariate (H6c and H8c respectively).”

Finally, upon revisiting our Results section, we noticed that we had not made it sufficiently clear that hypothesis H6a was preregistered as non-directional. We have now clarified this on page 9:

“We predicted that the metacognitive bias would correlate negatively with AD (Hypothesis 8a; more anxious-depressed individuals tend to be underconfident). For CIT, we preregistered a non-directional, significant link with metacognitive bias (Hypothesis H6a). We found support for both hypotheses, both for AD, β = -0.22, SE = 0.04, t = -5.00, p < 0.001, as well as CIT, β = 0.15, SE = 0.05, t = 3.30, p = 0.001, controlling for age, gender, and educational attainment (Figure 3; see also Table S1). Note that for CIT this effect was positive, more compulsive individuals tend to be overconfident.”

(3) You say special circles are red, blue, or pink. Then, in the figure, the colors are cyan, orange, and magenta. These should be homogenized. 

Apologies, this was not clear on our screens. We have corrected this now but used the labels “blue”, “orange” and “magenta” as our shade of blue is much darker than cyan:

Page 16: “These circles flashed in a colour (blue, orange, or magenta) when they first appear on screen before fading to yellow.”

(4) The task is not clearly described with respect to forced choice. From my understanding, "forced choice" was implicitly delivered by a "computer choosing for them". You should indicate in the graphic that this is what forced choice means in the graphic and description more clearly. 

This is an excellent point. On pages 17 and 18 we now include a slightly changed Figure 6, which includes improved table row names and cell shading to indicate the choice people gave. Hopefully this clarifies what “forced choice” means.

(5) If I have point (4) right, then a potential issue arises in your design. Namely, if a participant has a bias to use or not use reminders, they will experience more or less prediction errors during their forced choice. This kind of prediction error could introduce different mood impacts on subsequent performance, altering their accuracy. This will have an asymmetric effect on the different forced phases (ie forced reminders or not). For this reason, I think it would be worthwhile to run a version of the experiment, if feasible, where you simply remove choice prior to revealing the condition. For example, have a block of choices where people can "see how well you do with reminders" -- this removes expectation and PE effects. 

[See also this point from the weaknesses listed in the public comments:]

Although I think this design and study are very helpful for the field, I felt that a feature of the design might reduce the tasks's sensitivity to measuring dispositional tendencies to engage cognitive offloading. In particular, the design introduces prediction errors, that could induce learning and interfere with natural tendencies to deploy reminder-setting behavior. These PEs comprise whether a given selected strategy will be or not be allowed to be engaged. We know individuals with compulsivity can learn even when instructed not to learn (e.g., Sharp, Dolan, and Eldar, 2021, Psychological Medicine), and that more generally, they have trouble with structure knowledge (eg Seow et al; Fradkin et al), and thus might be sensitive to these PEs. Thus, a dispositional tendency to set reminders might be differentially impacted for those with compulsivity after an NPE, where they want to set a reminder, but aren't allowed to. After such an NPE, they may avoid more so the tendency to set reminders. Those with compulsivity likely have superstitious beliefs about how checking behaviors leads to a resolution of catastrophes, which might in part originate from inferring structure in the presence of noise or from purely irrelevant sources of information for a given decision problem. 

It would be good to know if such learning effects exist if they're modulated by PE (you can imagine PEs are higher if you are more incentivized - e.g., 9 points as opposed to only 3 points - to use reminders, and you are told you cannot use them), and if this learning effect confounds the relationship between compulsivity and reminder-setting.

We would like to thank the reviewer for providing this interesting perspective on our task. If we understand correctly, the situation most at risk for such effects occurs when participants choose to use a reminder. Not receiving a reminder in the following trial can be seen as a negative prediction error (PE), whereas receiving one would represent the control condition (zero PE). Therefore, we focused on these two conditions in our analysis.

We indeed found that participants had a slightly higher tendency to choose reminders again after trials where they successfully requested them compared to after trials where they were not allowed reminders (difference = 4.4%). This effect was statistically significant, t(465) = 2.3, p = 0.024. However, it is important to note that other studies from our lab have reported a general, non-specific response ‘stickiness,’ where participants often simply repeat the same strategy in the next trial (Scarampi & Gilbert, 2020), which could have contributed to this pattern.

When we used CIT to predict this effect in a simple linear regression model, we did not find a significant effect (β = -0.05, SE = 0.05, t = -1.13, p = 0.26).

To further investigate this and potentially uncover an effect masked by the influence of the points participants could win in a given trial, we re-ran the model using a logistic mixed-effects regression model. This model predicted the upcoming trial’s choice (reminder or no reminder) from the presence of a negative prediction error in the current trial (dummy variable), the ztransformed number of points on offer, and the z-transformed CIT score (between-subject covariate), as well as the interaction of CIT and negative PE. In this model, we replicated the previous ‘stickiness’ effect, with a negative influence of a negative PE on the upcoming choice, β = -0.24, SE = 0.07, z = -3.44, p < 0.001. In other words, when a negative PE was encountered in the current trial, participants were less likely to choose reminders in the next trial. Additionally, there was a significant negative influence of points offered on the upcoming choice, β = -0.28, SE = 0.03, z = -8.82, p < 0.001. While this might seem counterintuitive, it could be due to a contrast effect: after being offered high rewards with reminders, participants might be deterred from using the reminder strategy in consecutive trials where lower rewards are likely to be offered, simply due to the bounded reward scale. CIT showed a small negative effect on upcoming reminder choice, β = -0.06, SE = 0.04, z = -1.69, p = 0.09, indicating that participants scoring higher on the CIT factor tended to be less likely to choose reminders, thus replicating one of the central findings of our study. It is unclear why this effect was not statistically significant, but this is likely due to the limited data on which the model was based (see below). Finally, and most importantly, the interaction between the current trial’s condition (negative PE or zero PE) and CIT was not significant, contrary to the reviewer’s hypothesis, β = 0.04, SE = 0.07, z = 0.57, p = 0.57.

It should also be noted that this exploratory analysis is based on a limited number of data points: on average, participants had 2.5 trials (min = 0; max = 4) with a negative PE and 6.7 trials (min = 0; max = 12) with zero PE. There were more zero PE trials simply because to maximise the number of trials included in this analysis, each participant’s 8 choice-only trials were included and on those trials the participant always got what they requested (the trial then ended prematurely). Due to the fact that not all cells in the analysed design were filled, only 466 out of 600 participants could be included in the analysis. This may have caused the fit of the mixed model to be singular.

In summary, given that these results are based on a limited number of data points, some models did not fit without issues, and no evidence was found to support the hypotheses, we suggest not including this exploratory analysis in the manuscript. However, if we have misunderstood the reviewer and should conduct a different analysis, we are happy to reconsider.

Unfortunately, conducting an additional study without the forced-choice element is not feasible, as this would create imbalances in trial numbers for the design. The advantage of the current, condensed task is the result of several careful pilot studies that have optimized the task’s psychometric properties.

Scarampi, C., & Gilbert, S. J. (2020). The effect of recent reminder setting on subsequent strategy and performance in a prospective memory task. Memory, 28(5), 677–691. https://doi.org/10.1080/09658211.2020.1764974